acceptodds
Under review as a conference paper at ICLR 2027

Deep Sets GFlowNets for Subset Selection, with an Application to Combinatorial Chemistry

Abstract

DNA-encoded libraries (DELs) are combinatorial chemical libraries screened against a protein target in a single pooled experiment, avoiding the high costs associated with evaluating molecules one-by-one. We formulate DEL design as a combinatorial optimization problem which involves choosing sets of building blocks which produce many high-quality combinations. Generative Flow Networks (GFlowNets; Bengio et al. (2023)), which learn to sample compositional objects proportional to a reward, are well-suited to this problem, generating diverse, high-reward libraries rather than converging to a single optimum. However, applying GFlowNets to real-world DELs presents two open challenges: 1) DELs must be represented in a way that preserves the chemical structure of the underlying building blocks for efficient learning; 2) the cost of scoring candidate libraries must remain bearable at real-world scales. To address these obstacles, we leverage DeepSets representations to amortize the computation cost of combinatorial rewards and obtain a structure-aware GFlowNet architecture suitable for the optimization of combinatorial set functions on large structured environments. Applied to DEL design, our approach scales to libraries containing 125 billion elements, three orders of magnitude beyond prior work.

Primary area:
generative models
Keywords:
GFlowNets, Deep Sets, DNA-encoded libraries, combinatorial optimization, subset selection, active learning, multi-fidelity active learning, scalability, amortized inference, drug discovery, molecular discovery

Reviews

Among:
Shape:
1234this paper, Top 30%
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_XiRYOpenReview ↗
Rating
4(+1)
Confidence
3
Informativeness
3
Presentation
3
Soundness
3
Read review
Paper summary

The paper develops a method for reinforcement learning with a reward model that depends on combinatorial inputs, and applies it to design libraries of building blocks and reactions for synthesizing small molecules, in the context of DNA encoded libraries

Critical strengths

The paper addresses an important practical problem, that is critical for designing many actual wetlab experiments: how to select a subset of building blocks and reactions that it is tractable to implement in the wetlab. The approach they develop is principled and scalable, and will likely have interest beyond the specific problem of designing DELs, helping chemists choose which reactions to focus on and which building blocks to choose.

Critical weaknesses

The theory, in particular proposition 2, did not seem well motivated. The empirical results seemed to be missing important definitions. See questions below.

Questions for authors
  • The objective is not fully defined: How is it approximated from samples? What is Z_\theta, and how is it parameterized? As written, it seems to suggest we are minimizing over trajectories, but I believe you are actually minimizing over theta? To understand these points I had to look up the original trajectory balance paper - I think they should be clarified for the reader here.
  • What is the point of Proposition 2? Why does it matter that this map is injective? It appears related to the proof of DeepSets’ flexibility, but this is not explained.
  • Most important: What is the definition of diversity you are using and reporting in the experiments? How does the model promote structural diversity, if at all?
  • What is the subsampling rate? It seems to never be defined or explained.
  • What is the accuracy and performance of your surrogate model on its own? (Separate from the quality of the DEL designs.)
  • What efforts, if any, were made to ensure the reactions and building blocks were compatible with DEL chemistry? Many reactions are not tolerated in the context of DNA encoded small molecule libraries.

Minor suggestion: I think the problem setting might be explained more clearly to a wide audience by starting with the concrete DEL design problem, rather than beginning with the abstract definition of a c-structure, or at least specifying what is the c-structure of interest before the definition.

Overall, I think the paper is a valuable contribution, and will raise my score if the points above are addressed.

4 comments

We thank the reviewer for their detailed and constructive feedback. We address each question below. These changes appear in red in the updated manuscript.

Q1 (Objective is not fully defined):

We appreciate the reviewer for pointing out the lack of clarity in Section 3.1. We have since adjusted the main text to address each point.

"What is ZθZ_\theta, and how is it parameterized?"

We now define ZψZ_\psi (note a small non-substantive change to ψ\psi from θ\theta; this is a notational change only) where it first appears (Section 3.1), as the partition function of the flow network, that is the total flow leaving the initial state, Zψ=F(s0)Z_\psi = F(s_0), which equals ∑x∈XR(x)\sum_{x \in \mathcal{X}} \mathcal{R}(x) at the TB optimum. We note that it is learned directly as a single scalar parameter log⁡Zψ\log Z_\psi trained jointly with ψ\psi (again, previously denoted θ\theta, a notational change). The threshold-conditioned setting of Section 5.2 replaces this scalar with a small network taking a Fourier encoding of λ\lambda, as described there.

"As written, it seems to suggest we are minimizing over trajectories, but I believe you are actually minimizing over theta?"

The reviewer is correct that we minimize over ψ\psi (previously θ\theta), and our previous phrasing was ambiguous with regards to this point. We have separated the two statements that had been previously conflated. The guarantee is now stated as a condition; i.e., if Equation 1 is satisfied for every trajectory τ\tau, then the terminating distribution of PFP_F satisfies p(x)∝R(x)p(x) \propto \mathcal{R}(x). The optimization is stated separately, and explicitly identifies ψ\psi and log⁡Zψ\log Z_\psi as the variables being optimized rather than the trajectories themselves.

"How is it approximated from samples?"

We have added a description of the training procedure, which was previously excluded, in the paragraph following Equation 1 in Section 3.1. Since the constraint cannot be enforced over all τ\tau exactly, Equation 1 is used as a training objective, with trajectories sampled from the current PFP_F and stochastic gradient steps taken on the resulting loss with respect to ψ\psi and log⁡Zψ\log Z_\psi.

We have additionally clarified in the same subsection that ZψZ_\psi is the total flow out of s0s_0, learned as a single scalar parameter log⁡Zψ\log Z_\psi jointly with ψ\psi, and that in the combinatorial subset selection environments that we consider, all complete trajectories have the same length and PBP_B is uniform so the log PBP_B term is constant and absorbed into log⁡Zψ\log Z_\psi (with the argument given in Appendix C.3.4). We hope that the subsection is now readable without reference to [1].

Q2 (Additional clarity on the purpose of proposition 2):

The idea of viewing the soft count as a function of λ\lambda is to capture the empirical distribution of docking scores using a continuous function of λ\lambda, which is convenient to work with, and, most importantly, learnable by a neural network. The faithfulness of soft-count proposition is analogous to the uniqueness property of the Moment Generating Function (MGF): if XX and YY are random variables with equal moment generating functions, then XX and YY are equal in distribution. In this sense, the MGF is a functional avatar of a distributional object. Proposition 3 shows that the soft count enjoys a similar property, which justifies learning it as a function of λ\lambda, as we do in Section 5.2 (reward threshold conditioning) .

We thank the reviewer for pointing out that the justification for Proposition 2 (now Proposition 3 in restructuring) in the text was lacking. Since none of our results hinge on Propositions 2 and 3, which are purely intended as motivation, we have decided to move Propositions 2 and 3 to the Appendix, in Appendix A. The main text now instead clearly focuses on the ideas Proposition 2 and 3 were intended to convey, and refers the reader to the Appendix for technical details.

Q3 (Definition of diversity and does the model promote structural diversity?):

To directly answer the first query, "what is the definition of diversity you are using and reporting in the experiments?", we have adjusted the main text in Section 5.1, where we now state:

"We report diversity as the mean pairwise distance between the 100 highest-reward libraries, where each library is represented by concatenated mean Morgan fingerprints of its three building block pools and distances are computed with the Tanimoto coefficient (see Appendix C.3.3)."

A detailed description of precise calculation of diversity is also now provided in Appendix D.3.3.

(continued below)

Q4 (What is the subsampling rate? It seems to never be defined or explained):

The meaning of the subsampling rate has been clarified in the Section 5.1, stating:

"DeepSets-GFN parameterizes flows over (state, action) pairs, which allows the flow to be evaluated on a random subset of the available actions at each step rather than on the full action space (Seo et al., 2025). We refer to the fraction of actions retained as the subsampling rate psub∈(0,1]p_{sub} \in (0, 1] such that psub=1p_{sub} = 1 corresponds to evaluating every candidate building block and psub=0.02p_{sub}= 0.02, for example, corresponds to evaluating 2%2\% of them. This allows the per-step cost of training to be decoupled from the size of the building block pool."

Additionally, we have included detailed theoretical justification in Appendix C.4 D.

Q5 (Accuracy and performance of surrogate model on its own):

We report surrogate accuracy independently of DEL quality in Appendix D. The element-level docking proxy f^\hat{f} attains validation Pearson rr of 0.810.81--0.950.95 across the four targets (Table 4), and the library-level DeepSets model G^\hat{G} attains Kendall τ≈0.93\tau \approx 0.93 on held-out libraries (Table 5). Since G^\hat{G} serves as a ranking signal, we have added top-k%k\% overlap against the enumerated G~\tilde{G} on 100100K held-out libraries (Table 6), showing agreement of 0.900.90--0.910.91 at k=5%k = 5\% and strongest agreement in the upper tail, where it matters for training. Figure~2 further shows G^\hat{G}'s error decreasing over online learning iterations on an external stratified validation set.

Q6 (Efforts made to ensure the reactions and building blocks were compatible with DEL chemistry):

Our environments use building blocks from the Enamine catalog, with each having both a unique amine group and a unique acid group, assembled by amide coupling at both steps. Amide coupling is the most commonly used reaction in DEL synthesis [2], making the reaction chemistry in our environment representative of real DEL construction. Plainly, we made no effort to reject building blocks. We note that no general rule exists for predicting whether a given building block will be DEL-compatible; compatibility is established empirically, and even well-optimized on-DNA amidation consumes only 78% (423/543) of catalogue carboxylic acid substrates [3]. Restricting our pools to a validated subset would therefore have substantially narrowed the chemical space considered.

Ultimately, this work is primarily concerned with the combinatorial aspect of the DEL generation process, however it is possible to enforce any on-DNA compatibility criterion upstream of our pipeline by filtering building blocks prior to selection.

Additional suggestion (problem setting might be explained more clearly to a wide audience by starting with the concrete DEL design problem, rather than beginning with the abstract definition of a c-structure, or at least specifying what is the c-structure of interest before the definition)

Thank you for this suggestion! We have taken this into account and have updated the opening paragraph of Section 3 to specify what the cc-structure of interest is before the definition:

"Throughout, the cc-structure of interest is a tuple containing one building block from each pool, which corresponds to a single molecule of the resulting DEL"

We thank Reviewer XiRY for their attentive reading, and in particular for the suggestion to open the problem setting with the concrete DEL design problem rather than the abstract cc-structure definition --- a reframing that we think makes the paper substantially more accessible.

References

[1] Whitammer, Esmeralda S., et al. "Trajectory balance: Improved credit assignment in gflownets." Advances in neural information processing systems 35 (2022): 5955-5967.

[2] Hunter, James H., et al. “Highly efficient on-DNA amide couplings promoted by micelle forming surfactants for the synthesis of DNA encoded libraries.” Chemical Science 12.27 (2021): 9475-9484.

[3] Shi, Ying, et al. "DNA-encoded libraries (DELs): a review of on-DNA chemistries and their output." RSC advances 11.4 (2021): 2359-2376.

Thank you for the hard work and clear response; my concerns are addressed.

We thank reviewer XiRY and are grateful for their most helpful feedback.

Reviewer_fUkpOpenReview ↗
Rating
2
Confidence
4
Informativeness
3
Presentation
2
Soundness
2
Read review
Paper summary

The paper works on DNA-encoded library (DEL) design. The task is to choose subsets of building blocks from several pools. The chosen blocks give a combinatorial library of molecules, and this library should be rich in strong binders for one protein target. The authors name two problems for GFlowNets at real DEL scale. First, multi-hot action and state vectors throw away the chemistry of the building blocks. Second, the score of a library needs an evaluation of every molecule in it, and this cost grows multiplicatively with library size. The paper gives three answers. A smoothed soft-count reward (Eq. 3) removes regions with zero gradient. A DeepSets amortization predicts the library score from the sum of building block embeddings, so enumeration of all product molecules is not needed (Eq. 4, Prop. 3). A DeepSets-GFN architecture puts this representation into the state and action space of the GFlowNet, which permits action subsampling for large pools (Eq. 5). The experiments use four protein targets. The method beats two multi-hot GFlowNet baselines, MCMC and random search, and the gap grows with pool size. The authors describe the result as a search over about 125 billion candidate molecules.

Critical strengths
  • Clear problem formalization. The paper writes DEL design as subset selection over c-structures, then as a sequential decision problem (§2). This gives the rest of the paper a solid base. It is also not specific to DELs, as §6 says.
  • The soft-count reward is a useful trick. Eq. 3 and the bounds in Prop. 1 and Prop. 2 solve a real sparse reward problem, which the authors call "purgatory". Training would stall without it. The idea is small and portable, and other papers can use it.
  • The scaling comparison is the strongest result. Table 4 shows the multi-hot baselines get worse as the pool grows. DEL-GFN on ClpP goes 0.50, 0.56, 0.42 from small to large pools. DeepSets-GFN goes 0.50, 0.58, 0.60. This shows that a chemistry-aware representation matters more when the action space is larger.
  • Reproducibility is reasonable. Appendix D gives widths, hyperparameters and compute.
Critical weaknesses
  • Every number in Table 4 and Table 5 measures how well a method optimizes Ĝ. Ĝ is the same function the GFlowNet was trained to climb. This is the standard setup for reward hacking (Skalse et al., NeurIPS 2022; Gao, Schulman and Hilton, ICML 2023). A policy can learn the errors of the surrogate instead of the true objective. §5.3 adds an online learning loop, so the authors know this risk. But the main comparison in §5.1 does not appear to use online-corrected proxies. So I cannot see how much of the gap survives real docking. I suggest authors report real docking scores.

  • The proxy metrics look stronger than they are. The training set of f̂ is 500K random trimers. The training set of Ĝ is 500K random libraries. Both are uniform random, so most of the data is poor binders. MSE and soft-BCE fit this bulk first. A high global Pearson r (Table 2: 0.81 to 0.95) or Kendall τ (Table 3: about 0.92) can come mostly from separation of "bad" and "very bad". The tail near λ = −9 is the region the whole pipeline is built for, and the global number says little about it. This failure mode is known in imbalanced regression (Branco, Torgo and Ribeiro, ACM Computing Surveys 2016) and in virtual screening. Please report tail metrics, for example Spearman r or recall@k on the true top-k% of each training set.

  • The 125 billion claim compares two different quantities. Prior work reports 1.58 million molecules (§3.1). That space is enumerated, and the baselines hold all proxy values in memory. This paper's 125 billion (5,000³) is the size of the action space. The method never enumerates it, and that is the purpose of the amortization. So "three orders of magnitude beyond prior work" is not a fair comparison. By the same logic an atom-based GFlowNet (Pandey et al., ICML 2025) can claim 10$^{60}$ molecules, because that number is a property of the grammar and not of what is generated or scored. Please report what fraction of the 125B space was sampled during training, or state plainly that the claim is about representable action-space size.

  • Vina is a weak ground truth and the paper does not treat it as a limitation. AutoDock Vina scores correlate only loosely with real binding affinity, in particular across diverse molecule sets (Warren et al., J. Med. Chem. 2006; Pantsar and Poso, Molecules 2018). The authors acknowledge one such bias in Appendix D.3.1. It has a molecular weight correction, because "larger molecules are more likely to result in artificially good docking scores that do not reflect true binding affinity". This caveat belongs in the limitations, as a limit on the whole pipeline. Experimental validation is out of scope for this paper, and that is acceptable, but the paper should say so.

  • One global threshold for four targets. λ = −9 is used everywhere with no calibration argument. Docking score magnitudes are not comparable between targets. They depend on pocket size, polarity and scoring function bias. The per-target histograms in Appendix E.1 suggest the distributions differ. One absolute λ then puts each target at a different point of its own distribution, and the cross-target comparison becomes unclear. The paper already builds threshold conditioning (§5.2, Eq. 6), so it could set λ per target as a percentile of that target's random-sample distribution. The main comparison does not use this.

Questions for authors

Please see weakness section

5 comments

We thank the reviewer for their detailed and constructive feedback, and we address each comment below. These changes appear in red in the updated manuscript.

W1 (Results evaluated on the training surrogate; request for real docking scores):

The reviewer is entirely correct to point out that reward hacking can occur when surrogates are used as the training signal. The experiment of Section 5.1 was primarily intended to compare the methods in their ability to learn from a training signal, rather than intended as a full evaluation of the pipeline against the ground truth, which is itself a surrogate for true docking affinity which can only be measured in the wet-lab. Nevertheless, we recognize that the reviewer's interest in the performance of the methods as measured by the docking oracle is entirely justified and natural. For this reason, we have re-run the experiment of Section 5.1 in its entirety, using complete evaluation metrics: not only G^\hat G, but also G~\tilde G and the ground-truth GG using real docking scores. We used the 6-mean leaders of each method's top-100 for ground-truth evaluation, which amounts to roughly 450K450K docking runs per target. We increased the number of seeds from 3 to 5 in order to account for the additional noise which going down to the ground truth entails. The experiment is now complete and the manuscript has been updated; the ground-truth results across all three environments are as follows:

Mean docking reward exp⁡(G)\exp(G) of the 6-mean leaders of the top-100 (normalized ×10−3\times 10^{-3}, mean (std) over 5 seeds).

DS-GFNDS-GFN (0.02)DEL-GFNH-DEL-GFNMCMC
ClpP-2000.64 (0.010)0.61 (0.007)0.64 (0.009)0.58 (0.016)0.62 (0.015)
ClpP-10000.62 (0.010)0.59 (0.015)0.60 (0.012)0.55 (0.011)0.62 (0.019)
ClpP-45000.69 (0.004)0.67 (0.008)0.49 (0.028)0.44 (0.056)0.66 (0.016)
Mpro-2000.38 (0.003)0.38 (0.009)0.39 (0.008)0.38 (0.010)0.39 (0.015)
Mpro-10000.24 (0.005)0.33 (0.011)0.25 (0.017)0.29 (0.004)0.23 (0.021)
Mpro-45000.41 (0.010)0.37 (0.011)0.34 (0.085)0.30 (0.085)0.35 (0.029)
sEH-2000.59 (0.006)0.56 (0.010)0.60 (0.009)0.55 (0.012)0.59 (0.011)
sEH-10000.57 (0.013)0.55 (0.009)0.55 (0.011)0.53 (0.021)0.54 (0.019)
sEH-45000.64 (0.033)0.58 (0.023)0.53 (0.038)0.56 (0.017)0.59 (0.022)
TBLR1-2000.44 (0.004)0.42 (0.008)0.43 (0.008)0.42 (0.008)0.42 (0.015)
TBLR1-10000.44 (0.009)0.39 (0.006)0.41 (0.011)0.34 (0.008)0.40 (0.010)
TBLR1-45000.44 (0.015)0.42 (0.011)0.36 (0.038)0.29 (0.148)0.42 (0.022)

The DeepSets-based approach continues to outperform the multihot and hierarchical versions on the ground-truth metric, matching or exceeding both in 9 of 12 settings on the mean of leaders and 11 of 12 on the top-1 leader (Table 11), with the margin widening in the large environment where both baselines degrade sharply. Two of the three exceptions, CLpP-200 and Mpro-200, are differences of 0.010.01 within the seed spread. The third, Mpro-1000, does point in the direction of reward hacking, as the reviewer anticipated: deepsets attains the highest G^\hat G of any method there and the lowest GG, while the subsampled variant inverts this. We now discuss this case at length in Appendix D.3.1, where we locate the disagreement between G^\hat G and G~\tilde G rather than between f^\hat f and the oracle, and note that the higher-diversity subsampled policy is the one that resists the effect, which suggests that diversity-promoting mechanisms may offer some protection against surrogate exploitation.

W2 (Global correlations don't reflect surrogate accuracy in the high-affinity tail; request for tail metrics):

We thank the reviewer for this subtle point regarding the evaluation of the performance of the DeepDEL proxy model G^\hat G. We have an additional evaluation on the performance of the proxy on the upper tail, where it matters most for its use as a reward. From a set of 100K randomly sampled libraries, disjoint from the training data, we compared the top-k% as selected by G^\hat G and by G~\tilde G. As Table 6, which we reproduce below, shows, there is excellent agreement between the two selections of the top-k%.

Overlap between top-k%

0.2% (n=200)1% (n=1000)5% (n=5000)
CLpP167 (0.835)870 (0.870)4552 (0.910)
Mpro177 (0.885)877 (0.877)4558 (0.912)
sEH156 (0.780)848 (0.848)4518 (0.904)
TBLR1157 (0.785)864 (0.864)4513 (0.903)

(continued below)

W3 (The 125B versus 1.58M comparison conflates action-space size with enumerated search space; request to report the sampled fraction or rescope claim):

We thank the reviewer for this comment, which helped us realize that our comparison with prior work was not as clearly stated as it should have been. The 101110^{11} figure in our work is indeed comparable to the 10610^6 figure in prior work; both sizes represent the size of the entire top-level library, ∣B1∣×∣B2∣×∣B3∣|\mathcal B_1| \times |\mathcal B_2| \times |\mathcal B_3| (or in our case simply ∣B∣3|\mathcal B|^3 since the same pool is used across cycles). This is distinct from the action space, which is identified with the disjoint union B1⊔B2⊔B3\mathcal B_1 \sqcup \mathcal B_2 \sqcup \mathcal B_3, which has size ∣B1∣+∣B2∣+∣B3∣|\mathcal B_1| + |\mathcal B_2| + |\mathcal B_3| (or in our case simply 3∣B∣3|\mathcal B|). In the text, we have modified the wording of our comparison with prior work in order to provide additional clarity on this point. We note also that the building-block pool is now 4,699 monomers rather than 5,056, following removal of lingering duplicates, so the corresponding top-level library is ≈1011\approx 10^{11} rather than the 125 billion originally quoted.

W4 (Vina is a weak ground truth; request to move this into limitations):

We thank the reviewer for this point and we agree that the reliance on AutoDock Vina should be stated as a limitation on the pipeline, and have added this to Section 6. We do wish to clarify, however, that it bounds this particular instantiation rather than the central contributions themselves. Vina enters the pipeline as the scoring function ff on individual cc-structures, and each of our contributions sits strictly above it. Substituting a more faithful oracle changes only the values in the training set, not the aggregation, the amortization, or the architecture. What Vina bounds is the chemical interpretation of our reported numbers, rather than the validity of the methods that produced them.

W5 (Uncalibrated global threshold λ=−9\lambda = -9 is applied to all four targets with differing score distributions; suggestion to set λ\lambda per-target by percentile):

We thank the reviewer for this observation, which is entirely correct. We have addressed this by re-running the experiment of Section 5.1 using target-specific values for λ\lambda, namely the 25th percentile of docking scores observed in each docking proxy's training data. The values of λ\lambda thus obtained are −8.5-8.5, −8.23-8.23, −9.7-9.7, −9.08-9.08 for the targets ClpP, Mpro, sEH, and TBLR1, respectively, as illustrated in Figure 5. The re-run is now complete and the manuscript has been updated. Experiment 1 now reports 3 metrics over the same 12 settings: the DeepDEL reward G^\hat G (Tables 7-8), the enumerated docking-proxy reward G~\tilde G (Tables 9-10), and the ground-truth docking reward GG (Tables 11-12), so that the effect of the calibrated thresholds can be read at every level of the pipeline. The full G^\hat G results using these corrected values of λ\lambda are as follows; the corresponding ground-truth results appear in our response to W1 above.

Mean top-100 DeepDEL reward (normalized ×10−3\times 10^{-3}, mean (std) over 5 seeds).

DS-GFNDS-GFN (0.02)DEL-GFNH-DEL-GFNMCMC
ClpP-2000.59 (0.001)0.54 (0.004)0.59 (0.002)0.50 (0.002)0.58 (0.007)
ClpP-10000.64 (0.002)0.59 (0.001)0.63 (0.009)0.56 (0.002)0.63 (0.009)
ClpP-45000.70 (0.003)0.65 (0.005)0.49 (0.032)0.55 (0.010)0.65 (0.008)
Mpro-2000.48 (0.001)0.45 (0.002)0.48 (0.001)0.46 (0.003)0.47 (0.002)
Mpro-10000.64 (0.002)0.56 (0.003)0.62 (0.010)0.55 (0.003)0.61 (0.013)
Mpro-45000.61 (0.001)0.58 (0.004)0.48 (0.025)0.55 (0.033)0.58 (0.012)
sEH-2000.53 (0.001)0.48 (0.002)0.53 (0.001)0.47 (0.012)0.53 (0.003)
sEH-10000.63 (0.002)0.58 (0.004)0.62 (0.003)0.58 (0.005)0.63 (0.011)
sEH-45000.66 (0.005)0.62 (0.006)0.51 (0.035)0.57 (0.004)0.63 (0.017)
TBLR1-2000.46 (0.001)0.41 (0.002)0.45 (0.002)0.41 (0.008)0.45 (0.005)
TBLR1-10000.51 (0.001)0.46 (0.002)0.49 (0.011)0.44 (0.002)0.50 (0.007)
TBLR1-45000.50 (0.001)0.47 (0.004)0.38 (0.034)0.41 (0.009)0.49 (0.020)

Under the calibrated thresholds, deepsets matches or exceeds both GFlowNet baselines in all twelve settings on this metric, with the margin over multihot widening sharply in the large environment on every target.

We thank Reviewer fUkp for their careful reading, and in particular for the point that our global proxy metrics say little about the tail --- a gap we have now addressed with tail-specific metrics, alongside the complete ground-truth evaluation and threshold calibration described above.

The experiments promised in our previous comments are now complete and our responses have been edited to reflect the final results; we thank reviewer fUkp for their patience. We remain available to answer any additional questions.

Reviewer_6aYGOpenReview ↗
Rating
2
Confidence
4
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

The paper combines a DeepSets library-reward surrogate with a feature-aware GFlowNet for combinatorial subset selection. It evaluates DEL design across four protein targets and three pool sizes, with extensions for threshold conditioning and online surrogate refinement.

Critical strengths
  1. The problem is useful and clearly motivated.
  2. Feature-aware set and action representations are sensible.
  3. Results show encouraging improvements over DEL-GFN in larger environments.
Critical weaknesses
  1. Independent evaluation is unclear.** Section 5.1 refers to docking scores, while Figure 1 and Table 4 report DeepDEL rewards. It is unclear whether optimized libraries are evaluated using G^\hat G, enumerated docking-proxy scores, or actual docking. Surrogate exploitation therefore remains insufficiently addressed.
  2. Scalability lacks complete accounting.** The 125-billion figure concerns the candidate universe, not generated library size. Surrogate data construction and training costs are substantial but not reported.
  3. Novelty is mainly architectural and integrative. Ablations are needed to separate benefits from molecular features, DeepSets aggregation, and state–action modeling.
  4. Mathematical and implementation details need correction. Proposition 1 (Line 264) has the wrong exponent sign in ϵδ\epsilon_\delta and omits the reward’s additive 11 from its upper bound. Section 5 incorrectly writes exp⁡(G^)≈log⁡r\exp(\hat G)\approx\log r, rather than rr (Line 357). Action-subsampling probabilities and the effective reward with β=200\beta=200 also need clarification.
Questions for authors
  1. Do the reported improvements persist under enumerated proxy evaluation and independent docking?
  2. What are the end-to-end computational costs?
  3. How are trajectory probabilities computed under action subsampling?
  4. Can matched-budget ablations isolate the proposed architectural and pretraining benefits?
6 comments

We thank the reviewer for their detailed and constructive feedback, and we directly address each stated weakness and question below. These changes appear in red in the updated manuscript.

W1 (Evaluation metric is ambiguous and surrogate exploitation unaddressed):

This arises from inconsistent terminology on our part. To clarify, our pipeline involves three distinct quantities, including: 1) the AutoDock Vina oracle ff, 2) the learned element-level proxy f^\hat f, which defines the exact soft count r~\tilde r over all enumerated trimers, and 3) the DeepSets amortization (reward) G^≈log⁡r~\hat G \approx \log \tilde r, which is the quantity that the GFlowNet optimizes.

The references to "docking scores" and "docking rewards" in Sections 1 and 5.1 were imprecise and have been corrected, so that each reported quantity is now named by what it measures.

The reviewer is correct to point out that reward hacking could potentially occur when surrogates are used as the training signal. The experiment of Section 5.1 was primarily intended to compare the methods in their ability to learn from a training signal, rather than as a full evaluation of the pipeline against the ground truth (itself a surrogate for true binding affinity, which can only be measured in the wet lab). Nevertheless, we recognize that the reviewer's interest in the performance of the methods as measured by the docking oracle is entirely justified.

We have therefore re-run Experiment 1 in its entirety and now report three metrics over the same twelve settings: the DeepDEL reward G^\hat G (Tables 7-8), the enumerated docking-proxy reward G~\tilde G (Tables 9-10), and the ground-truth docking reward GG obtained from AutoDock Vina (Tables 11-12). Ground-truth evaluation uses the 6-mean leaders of each method's top-100, which required on the order of 450,000 docking runs per target. The number of seeds was increased from 3 to 5 to account for the additional noise that going down to the ground truth entails. Under the ground-truth docking reward, DeepSets-GFN matches or exceeds both GFlowNet baselines in 9 of 12 settings on the mean of leaders (reproduced below) and in 11 of 12 on the top-1 leader (Table 11), and in all four of the largest environments under either measure. Two of the three exceptions below, Mpro-200 and sEH-200, are differences of 0.010.01 that fall within the seed spread; the third, Mpro-1000, is discussed separately.

Mean docking reward exp⁡(G)\exp(G) of the 6-mean leaders of the top-100 (normalized ×10−3\times 10^{-3}, mean (std) over 5 seeds).

DS-GFNDS-GFN (0.02)DEL-GFNH-DEL-GFNMCMC
ClpP-2000.64 (0.010)0.61 (0.007)0.64 (0.009)0.58 (0.016)0.62 (0.015)
ClpP-10000.62 (0.010)0.59 (0.015)0.60 (0.012)0.55 (0.011)0.62 (0.019)
ClpP-45000.69 (0.004)0.67 (0.008)0.49 (0.028)0.44 (0.056)0.66 (0.016)
Mpro-2000.38 (0.003)0.38 (0.009)0.39 (0.008)0.38 (0.010)0.39 (0.015)
Mpro-10000.24 (0.005)0.33 (0.011)0.25 (0.017)0.29 (0.004)0.23 (0.021)
Mpro-45000.41 (0.010)0.37 (0.011)0.34 (0.085)0.30 (0.085)0.35 (0.029)
sEH-2000.59 (0.006)0.56 (0.010)0.60 (0.009)0.55 (0.012)0.59 (0.011)
sEH-10000.57 (0.013)0.55 (0.009)0.55 (0.011)0.53 (0.021)0.54 (0.019)
sEH-45000.64 (0.033)0.58 (0.023)0.53 (0.038)0.56 (0.017)0.59 (0.022)
TBLR1-2000.44 (0.004)0.42 (0.008)0.43 (0.008)0.42 (0.008)0.42 (0.015)
TBLR1-10000.44 (0.009)0.39 (0.006)0.41 (0.011)0.34 (0.008)0.40 (0.010)
TBLR1-45000.44 (0.015)0.42 (0.011)0.36 (0.038)0.29 (0.148)0.42 (0.022)

Mpro at the medium pool size is the one setting where the three metrics disagree substantively: DeepSets-GFN attains the highest DeepDEL reward of any method there and the lowest docking reward, while the subsampled variant inverts this (0.330.33 against 0.240.24 in the table above). We discuss this case at length in Appendix D.3.1, where we argue that it is best read as reward hacking, locate the disagreement between G^\hat G and G~\tilde G rather than between f^\hat f and the oracle, and note that the higher-diversity subsampled policy is the one that resists the effect, which suggests that diversity-promoting mechanisms may offer some protection against surrogate exploitation.

W2 (Scalability lacks complete accounting):

It is correct to say that the figure we quoted describes the candidate space from which libraries are selected rather than the size of a generated library; the generated libraries presented in this work are 10x10x10. We have adjusted the abstract to instead reflect, more generally, that:

"...our approach scales to arbitrarily large selection environments, overcoming the limitations of prior enumerative, structure-blind methods."

(continued below)

We have also added the term "top-level" when citing the 1.58M figure in Section 3, so that it is clear the comparison is between candidate spaces of the same kind and that the "three orders of magnitude" claim can be checked directly.

We note that what scales in our setting is the space searched rather than the output. The generated libraries contain 1000 compounds, but they are selected from an action space of 4500 building blocks in the large environment, and scored without ever enumerating the proxy over the full top-level library, which is the step that confined prior work to at most 1.58M compounds.

Regarding the surrogate data construction and training costs, we have added two detailed compute tables (Table 2 and Table 3) to Appendix C.4.1. Table 2 reports approximate stage-by-stage compute cost per target. We observe that lower action subsampling rates (psubp_{\text{sub}}) greatly reduce the cost of GFN training. Table 3 reports resource totals for a single online learning run consisting of 100K total trajectories. Both tables are shown below.

Table 1: Approximate stage-by-stage compute cost per target. CPU entries are core-hours; GPU entries are MIG-slice GPU-hours (single GPU node). Costs are reported for both 10×10×1010 \times 10 \times 10 and 20×20×2020 \times 20 \times 20 libraries. The bottom two lines illustrate how action subsampling greatly reduces the cost of GFN training.

StageResource10×10×1010\times10\times1020×20×2020\times20\times20
Vina docking (500K)CPU20,00020,000
Autodock proxy trainingGPU22
DeepDEL dataset constructionCPU5004,000
DeepDEL trainingGPU0.51
GFN training, subsample 0.02GPU1122
GFN training, subsample 1.00GPU78156

Table 2: Resource totals for a single online learning run consisting of 100K total trajectories. Cost: GPU rows in GPU-hours; CPU rows in core-hours. Wall clock is in hours, reported separately for 10×10×1010\times10\times10 (10310^3) and 20×20×2020\times20\times20 (20320^3) libraries. Highly parallelizable stages assume 200 ×\times 64 cores using concurrent sharding (docking and dataset generation). CPU tasks during GFlowNet training, such as library enumeration when using reward G~\tilde G, are assumed to be poorly parallelizable, assuming that 48 CPUs are available on the GPU node used for training. The bottom two lines illustrate the impact of combinatorial amortization; when using G~\tilde G, the CPU wall-clock time scales with ℓ3\ell^3, whereas it scales with ℓ\ell when using the non-enumerative DeepDEL proxy G^\hat G.

ComponentCost (10310^3)Cost (20320^3)Wall clock, h (10310^3)Wall clock, h (20320^3)
GPU (GPU-h)
Autodock proxy + DeepDEL training2.532.53
GFN policy, subsample 0.0211221122
GFN policy, subsample 1.007815678156
GPU total, subsample 0.0213.52513.525
GPU total, subsample 1.0080.515980.5159
CPU (core-h)
Vina docking (highly parallelizable)20,00020,00022
DeepDEL dataset (highly parallelizable)5004,0000.51.5
GFN enumeration (poorly parallelizable, 48 CPU)3002,850660
CPU total, G^\hat G log-reward20,50024,0002.53.5
CPU total, G~\tilde G log-reward20,80026,8508.563.5

W3 (Novelty is mainly architectural and integrative; ablations are needed):

We thank the reviewer, whose comment points to an imbalance between the weight the manuscript gives the architecture and the weight it gives our contribution to amortized inference. Beyond the architecture, we contribute a general scheme for amortizing combinatorial set functions, justified by Proposition 1, which scores a reward defined over a combinatorial structure directly from the building blocks without enumerating it. This removes library enumeration from GFlowNet training, and applies to any reward decomposing over a combinatorial structure on sets, not only to DELs. We have revised the text accordingly and added compute estimates with and without amortization (Table~3): on 100100K trajectories over 20×20×2020 \times 20 \times 20 libraries, CPU wall-clock drops from 63.563.5h to 3.53.5h, a saving scaling with ℓ3\ell^3.

(continued below)

On the ablations: we attempted this factorial study before concluding the three factors cannot be separated informatively. Our one substantive commitment is that the policy see the chemical identity of building blocks rather than their indices; the other two mechanisms follow. A state is a set of fingerprints, so the encoder must pool them invariantly; short of DeepSets one fixes an order and concatenates, giving 2048×(ℓ1+ℓ2+ℓ3)2048 \times (\ell_1 + \ell_2 + \ell_3) inputs that exhaust the equalized parameter budget in the first layer. A fixed ∣B∣|\mathcal{B}|-way head, likewise, indexes actions by position and cannot consume an action's fingerprint, so it withdraws molecular features rather than holding them fixed. Conversely, with no features ϕ\phi reduces to an embedding table over indices and ∑b∈Bϕ(b)\sum_{b \in B} \phi(b) is a learned linear map on the multi-hot indicator of BB --- DEL-GFN with its first layer renamed. Avoiding that collapse means picking something else to feed the aggregator, each choice carrying its own ablation. We therefore read DEL-GFN as the molecular-feature ablation of our model rather than a competing baseline, with H-DEL-GFN the intermediate recovering structure coarsely through clustering, parameter counts equalized to within 1%1\%. This matches our actual claim, which is not that each mechanism helps at fixed scale but that structure awareness preserves performance as the action space grows: the models are close in the small environment (ClpP 0.500.50 for both), whereas in the large one DEL-GFN degrades (ClpP 0.420.42 vs 0.600.60; Mpro 0.240.24 vs 0.420.42) and ours improves. We would welcome a specific variant if the reviewer thinks one would be diagnostic.

W4 (Mathematical and implementation details need correction):

To address the first point, Proposition 2 (sandwich inequality) has now been updated to correct the sign in the exponent, so that ϵδ=σ(−δ/h)=(1+eδ/h)−1\epsilon_\delta = \sigma(-\delta/h) = (1+e^{\delta/h})^{-1}, which matches the expression already used in the corresponding proof. The reviewer is also correct that the reward’s additive constant was omitted from the upper bound. We have restated the sandwich inequality so that the upper bound accounts for this constant:

(1−ϵδ)N(λ−δ):≤:rλ,h(x):≤:1+N(λ+δ)+nϵδ.(1-\epsilon_\delta)N(\lambda-\delta)\\: \leq\\: r_{\lambda, h}(x)\\: \leq\\: 1 + N(\lambda+\delta) + n\epsilon_\delta.

The note on exp⁡(G^)≈log⁡r\exp(\hat G) \approx \log r in Section 5 has also been corrected.

To address the reviewer's comment that "action-subsampling probabilities and the effective reward with β=200\beta = 200 also need clarification", we have added the following in Section 5:

“In all experiments, we apply an inverse-temperature exponent β=200\beta = 200, so the effective reward is R(x)=exp⁡(βG^(x))≈r(x)β\mathcal R(x) = \exp(\beta\hat G(x)) \approx r(x)^\beta. In all experiments, we apply an inverse-temperature exponent β=200\beta = 200, as is customary in GFlowNet training to sharpen the reward (Bengio, 2023); so the effective reward is R(x)=exp⁡(βG^(x))≈r(x)β\mathcal R(x) = \exp(\beta\hat G(x)) \approx r(x)^\beta. We swept β∈[1,500]\beta \in [1, 500] and selected β=200\beta = 200 as an adequate value that separated high- from low-reward libraries enough to drive learning without destabilizing training; in our experiments, it is used unchanged across all targets and environments.”

With regards to action-subsampling probabilities,the newly added Appendix D.3.5 provides further detail. At each step mk(s)m_k(s) actions per pool are drawn uniformly without replacement, the flow is evaluated only on those, and the total flow leaving ss is estimated by importance sampling with weight ∣Ak(s)∣/mk(s)|A_k(s)|/m_k(s). The estimator is unbiased; the logarithm leaves a small downward bias vanishing as mk(s)→∣Ak(s)∣m_k(s) \rightarrow |A_k(s)|, and at psub=1p_{\text{sub}} = 1, the expression reduces exactly to the softmax over A(s)A(s).

Q1 (Do reported improvements persist under enumerated proxy evaluations and independent docking?):

We thank the reviewer for this inquiry and address it above in response to W1.

(continued below)

Comments on the paper

2 comments
AuthorsOpenReview ↗

Response to all reviewers

We sincerely thank all three reviewers for their thorough and helpful feedback. Below, we discuss the changes made in this revision.

Reward models were re-trained using target-specific thresholds. In the initial submission, we applied a single cutoff (λ=−9\lambda = -9) across all four targets. As pointed out in the reviews, docking scores have different scales depending on the target, so a fixed cutoff sits at a different quantile for each target and skews cross-target comparisons. We now set λ\lambda to the 25th percentile of each target's docking-score distribution as displayed in the improved Figure 5 (λClpP=−8.5\lambda_{\text{ClpP}} = -8.5, λMpro=−8.23\lambda_{\text{Mpro}} = -8.23, λsEH=−9.7\lambda_{\text{sEH}} = -9.7, λTBLR1=−9.08\lambda_{\text{TBLR1}} = -9.08), retrained all reward models with these thresholds, and re-ran Experiment 1 using these models.

Experiment 1 re-run and evaluated using real docking scores. We no longer report only the learned surrogate G^\hat{G}. Instead, we re-scored the selected libraries with both the enumerated docking proxy exp⁡(G~)\exp(\tilde{G}) and the soft count of true Vina scores, exp⁡(G)\exp(G), evaluating the 6-means leaders of the top-100. Because ground-truth docking adds variance, we increased the number of seeds from 3 to 5. This evaluation required 1.8 million Vina calls in total (1,000 molecules per library across 6 leader libraries, 5 seeds, 5 methods, and 3 environment sizes per target). All three metrics (both top-1 and mean top-100 across the 12 settings) now appear in Appendix D.3 (Tables 7--12). Under the ground truth, DeepSets-GFN matches or outperforms both GFlowNet baselines in 11 out of 12 settings, and leads across every metric in all four of the largest environments. We updated the introduction and S5.1 to frame our claims around docking scores instead of the surrogate reward.

Additional evaluation metrics. Global Pearson r and Kendall τ\tau do not capture accuracy in the upper tail, which is the regime our pipeline actually selects from. To evaluate tail agreement directly, Table 6 now includes top-kk\\% overlap between G^\hat{G} and G~\tilde{G} for k=0.2,1,5k=0.2,1,5 on a held-out set of 100K libraries, and we added an explicit pointer to these results in D.2.

Definitions and corrections. For transparency, we note that the building-block pool went from 5,056 to 4,699 monomers, and the large environment from 5,000 to 4,500 building blocks, as we removed lingering duplicates from the pool. We corrected the sign in ϵδ\epsilon_{\delta} and restored the additive 1 in the sandwich inequality's upper bound, fixed the exponent and indexing in the proof of Proposition~1, and resolved several inconsistencies in notation between the predictive (ρ,ϕ)(\rho, \phi) and generative (P,Φ)(P, \Phi) models, which are now distinguished explicitly. We clarified that the Trajectory Balance objective is minimized over the network parameters rather than over trajectories, and unified the kernel width as hh throughout, where some sections previously wrote HH. The diversity metric (C.3.3) and the subsampling rate (C.4) are now defined where they are first used rather than only in the appendix, and the problem setting names the concrete DEL design problem before introducing cc-structures. The Vina caveat, previously confined to an appendix, now appears in the Limitations as a limit on the whole pipeline. We also added captions to the per-target library figures in Appendix F, a legend for the bolding convention in the result tables, and the training budgets for the threshold-conditioning experiment.

Remaining items. Results on Mpro lag behind the other three targets across all metrics. We analyze this in Appendix D.3.1: the failure mode looks like reward hacking of the proxy, and the higher-diversity subsampled policy recovers substantially better docking scores on Mpro. This suggests that diversity-promoting methods help curb surrogate exploitation. Finally, we did not run matched-budget ablations separating molecular features, DeepSets aggregation, and state--action modeling; as explained in our reply to Reviewer 6aYG, these components are coupled in a way that makes isolated ablations hard to interpret in this setting.

Conclusion. With these revisions, our main claims are backed directly by ground-truth docking evaluations rather than proxy scores alone, and the paper's framing around amortized combinatorial inference is clearer. The relative ordering of methods holds under both the enumerated proxy and Vina itself, our gains are largest in environments where enumeration-based baselines are least usable, and the single target where metrics diverge (Mpro) is analyzed openly in the text. We appreciate the reviewers pushing us to include these experiments and believe the updated manuscript addresses their main concerns.

Changes from the original submission are marked in red throughout. Please let us know if any further questions remain.

This last revision contains minor fixes and cosmetic edits.

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

Related papers

Loading the map…

Discussion (0)

Sign in to comment.