acceptodds
Under review as a conference paper at ICLR 2027

DARPinBench: A Dataset and Library-Screening Benchmark for Designed Ankyrin Repeat Proteins

Abstract

Pulling a handful of experimentally confirmed binders to the front of a library whose members differ by one or two point mutations is a recurring machine-learning problem, from antibody affinity maturation to the triage step of a generative design pipeline. Designed ankyrin repeat proteins (DARPins) instantiate it: one shared solenoid scaffold, sparse positives, and negatives that are near neighbors. Public sources keep sequences, complex coordinates, and binding readouts apart, so neither an auditable table nor a frozen ranking protocol exists for this scaffold. We release both. DARPinDB annotates sequence, binding label, , and evidence source on a single record: 188 records, 179 binders, and 37 targets, of which 121 carry a numeric , with structures tiered and released with chain maps. DARPinBench freezes three screening modes on that table. Mode 1 scores ten mainstream methods from the sequence, structure, rescoring, and docking families on ten near-neighbor libraries of 500 sequences each; Modes 2 and 3 release a shared 20,000-member library and a leave-one-target-out split as held-out material, unscored here. No method reaches the top 1% of a library reliably: the best rate at the top 1% is of ten units, AF3 attains the highest recall at the top 10% () while reaching only at the top 1%, and the median enrichment factor at 5% is zero for eight of the ten methods. A high DockQ does not travel with a front-of-library rank. We introduce no new scorer; the contribution is a frozen reference line, together with a diagnosis of where off-the-shelf scores fail, for later evolution and training to exceed.

Primary area:
datasets and benchmarks
Keywords:
DARPin, designed ankyrin repeat proteins, protein-protein interaction, library screening, datasets and benchmarks, binder design, virtual screening, protein structure prediction, molecular docking

Reviews

Among:
Shape:
1234this paper, Bottom 27%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.00 over 3 reviews, above 27% of the others.
Reviewer_UWL3OpenReview ↗
Rating
2
Confidence
2
Informativeness
1
Presentation
3
Soundness
1
Read review
Paper summary

This work introduces DARPinDB, a curated collection of 188 DARPin-target records across 37 targets, and DARPinBench, a library-ranking benchmark. 10 methods are evaluated on 10, 500-candidate libraries. The main findings are inconsistent early retrieval of annotated binders and examples where accurate complex prediction does not translate into favorable library rank. Two additional large-library and cross-target protocols are released without results.

Critical strengths

• The paper is generally easy to follow

• Establishing curated benchmarks is important for reliable evaluation and development of scoring models

• The evaluation compares several scoring families on shared candidates and reports per-target results, uncertainty, and computational costs.

Critical weaknesses
  1. The negative labels limit the biological interpretation of the benchmark. This is my primary concern. Among 5,000 Mode 1 entries, only nine are experimentally confirmed nonbinders, all from BCL-W; 4,899 are synthetic candidates. Introducing one to three substitutions into a known binder does not establish loss of binding. Some variants could retain or improve binding, so ranking them highly may be useful experimentally while being penalized by the benchmark. Specific biological knowledge about this protein family as well as references to other fields where decoys are often created (pMHC benchmarks, DUD-E) would help to motivate the validity of these decoys and the methods used to generate them. A cheap construction audit should report pairwise Hamming distances (or other metrics) among each unit’s positives and each decoy’s distance to its second-nearest positive, where available. These would expose positive redundancy and overlapping mutation neighborhoods, although sequence proximity alone cannot establish whether a candidate binds.

  2. The paper contributions are only partially demonstrated. The curated dataset is a useful contribution. However, two of the three proposed benchmark modes (modes 2 and 3) are released without experiments, leaving their usefulness for large-library screening and cross-target learning unexplored. At least inexpensive reference methods should be evaluated, and the provenance of the shared library should be documented. Modes 2 and 3 are not well described, not executed and provide no new insights as currently presented. The ten-method reference comparison is also useful, but the claimed failure diagnosis provides limited additional insight. Its central observation (that accurate pose recovery does not guarantee favorable library ranking) is consistent with previous work distinguishing structural accuracy from binding and affinity prediction in other protein settings. Demonstrating this behavior for DARPins adds application-specific evidence, but the manuscript should clarify what new understanding follows: does failure arise from pose generation, the selected scoring functions, or insufficient target-specific discrimination? The current examples largely document the distinction without explaining it.

Questions for authors
  1. Why must targets have an experimental co-crystal to enter the ranking evaluation? Could the authors include the remaining eligible targets in the screening benchmark while restricting DockQ analysis to the anchored subset? Given the additional binding annotations and the uncertainty arising from only ten evaluated units, this could substantially improve coverage and precision without weakening the structural controls.
  2. Do timing comparisons include MSA searches and prerequisite pose generation, and what computations were cached or reused? Generating identical MSAs for proteins differing by 1-3 mutations unnecessarily inflates computational costs for structure based models.
  3. How are the replacement amino acids chosen when generating mutation decoys? Please specify the allowed amino-acid alphabet and sampling distribution, and whether substitutions are constrained by position or physicochemical properties. Do the generated decoys follow the position-specific amino-acid preferences of the intended DARPin libraries? Introducing residues rarely observed at these positions could create shortcuts that models can take advantage of.
  4. Do the mutated residues lie at the DARPin-target interface in the predicted complexes? Reporting this fraction and its relationship to score changes would help distinguish incorrect interface placement from limited sensitivity to mutations within the interface.
  5. How do score changes and retrieval performance vary with mutation count (k∈[1,2,3]k \in [1,2,3]) within each target? This would help characterize sensitivity to progressively larger sequence perturbations.
  6. Could the authors include random-ranking success rates alongside the Top-k results, accounting for each unit’s number of positives? This would help readers assess the improvement over chance.
2 comments

Dear Reviewer UWL3,

Our revised PDF is now online, with changes marked in blue. Following your review, the construction audit of the synthetic candidates and the position-profile baseline are added; the random-ordering null appears in Figure 3b; Modes 2 and 3 have reference scores; a figure stratified by the number of substitutions (k) covers all ten methods; the timing paragraph in Section 4 states what each hour includes; and the Limitations section states the admission criterion for units.

We hope the revision addresses your concerns and look forward to your feedback. If anything else should be changed, we will do our best to address it before the deadline.

Thank you for the detailed and constructive review.

Dear Reviewer UWL3,

A gentle reminder that our revised PDF has been online since 13 November, with changes marked in blue. It includes the construction audit of the synthetic candidates, the position-profile baseline, and the mutation-stratified retrieval analysis you asked about.

The discussion period closes on 18 November (AoE), so time is getting short. If you have a moment, we would appreciate your feedback and, if the revision addresses your concerns, an updated assessment. If anything else should change, a note in the next day would let us address it before the deadline.

Thank you for your time.

Reviewer_Hr8kOpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

The paper introduces DARPinDB and DARPinBench, a dataset and benchmark for evaluating computational screening of designed ankyrin repeat protein (DARPin) binders. DARPinDB contains 188 records covering 179 binders and 37 targets, with 121 records containing numerical binding affinities and additional annotations for structural information and evidence sources. DARPinBench defines three screening modes: near-neighbor library ranking (Mode 1), shared-library screening (Mode 2), and leave-one-target-out generalization (Mode 3). The authors evaluate ten methods across sequence, structure prediction, rescoring, and docking on ten libraries containing 500 candidates each in Mode 1. Modes 2 and 3 are released without baseline evaluations. Results show that existing methods struggle to identify experimentally labeled binders among near-neighbor candidates. The highest Top-1% success rate is 0.30, achieved by ProtT5, while AF3 achieves the highest Top-10% success rate of 0.80. The authors also analyze the relationship between structural prediction accuracy and library ranking, showing that accurate binding poses do not necessarily lead to better candidate prioritization.

Critical strengths
  • The paper addresses a practical problem in protein binder discovery by focusing on ranking candidates from libraries containing highly similar sequences, rather than general protein-protein interaction prediction.
  • DARPinDB integrates binder sequences, binding annotations, affinity measurements, structural information, and evidence sources into a curated dataset, which could be useful for future research on DARPin design and screening.
  • The benchmark evaluates diverse methods across sequence, structure prediction, rescoring, and docking, providing reference results for comparing different computational approaches.
  • The authors provide detailed analyses of early enrichment, computational cost, and structural prediction quality, including uncertainty estimates and per-target results. The distinction between pose recovery and library ranking is particularly informative.
Critical weaknesses
  • My main concern is the reliability of the negative labels used in the benchmark. DARPinDB contains only nine experimentally confirmed nonbinders, while most negative candidates in Mode 1 are synthetically generated decoys. In particular, many decoys are generated through one to three mutations, but these mutations do not necessarily eliminate binding activity. Although the authors distinguish synthetic decoys from experimentally confirmed negatives, treating these candidates as negatives may affect the interpretation of the reported screening results.
  • The benchmark evaluation is relatively small, covering only ten computational units from nine biological targets. Five units contain fewer than three positive binders, making the evaluation highly sensitive to individual ranking outcomes. Although the authors report confidence intervals, a larger and more diverse evaluation would strengthen the generalizability of the findings.
  • Modes 2 and 3 are introduced as shared-library screening and cross-target generalization benchmarks, but neither mode is evaluated in the paper. Moreover, a sequence is labeled as a binder only for its known target and treated as a task negative for other targets without necessarily having experimental evidence of nonbinding. This raises concerns about the reliability of the labels and the usefulness of these modes for evaluating cross-target generalization.
Questions for authors
  • In Appendix B.3, most negative candidates are synthetic decoys rather than experimentally verified nonbinders. Since mutations to known binders do not necessarily eliminate binding activity, how confident are the authors that these candidates should be treated as negatives? Could the authors provide a sensitivity analysis showing how the reported ranking results change under different compositions of synthetic decoys?
  • For Modes 2 and 3, a sequence is labeled as a binder only for the target where it was originally identified and treated as a task negative for other targets. How do the authors account for potential cross-target binding when constructing these labels? In particular, how might unobserved positive interactions affect the reliability of the leave-one-target-out evaluation?
3 comments
AuthorsOpenReview ↗

Response to Reviewer Hr8k: negative labels, benchmark size, Modes 2 and 3

Thank you for your questions about negative labels and Modes 2 and 3.

Negative labels (W1, Q1). We agree that mutations to a binder need not abolish binding. We will call the 2,753 k-mutants unlabelled synthetic candidates. The general comment gives the supporting references and a HER2 binding check: of 13 high-scoring decoys, one bound weakly (about 23.8 nM, roughly fivefold weaker than the two positives) and 12 showed no detectable binding.

For the sensitivity analysis you asked for, we changed the decoy composition four ways and compared method order with the original ranking (Spearman correlation of each method's total successes over the three budgets). Deleting k = 1 decoys (4,238 candidates left) gives 0.86; deleting k ≤ 2 decoys (3,481) gives 0.92; deleting decoys within normalized Hamming 0.02 of a positive (2,955) gives 0.90. Treating each k-mutant as a hidden binder with probability 0.05, 0.10, 0.20 or 0.30 gives 0.90, 0.78, 0.61 and 0.40, while the expected Top-10% success of random ordering rises from 4.14 to 9.26 at 0.20. Method order is stable under deletion and moderately stable up to a 10% hidden-binder rate. We will add this table to the appendix.

Size (W2). Ten units from nine targets is a small sample, five units have fewer than three positives, and the Wilson intervals are wide: success rates of 8/10 and 4/10 have 95% Wilson intervals of 0.49 to 0.94 and 0.17 to 0.69, respectively, which shows the limited precision of aggregate rates over ten units. The paper already marks units with fewer than three positives as high-variance, and the new null table will carry the same mark. DARPin research is still at an early stage and few DARPin-target complexes are known. We restrict Mode 1 to units anchored by an experimental co-crystal, which keeps the entries traceable and lets structure-based, sequence-based and classical methods be compared on the same libraries; the small size follows from this inclusion criterion. We will add the null and robustness tables so that readers can see each method's result relative to random ordering. We do not add units in this revision.

Modes 2 and 3 (W3, Q2). We scored both modes with inexpensive references. Mode 2 (20,000 sequences shared across the ten units): ESMC 1/2/2, ProtT5 1/4/6 and D-SCRIPT 2/3/5 of 10 units at Top-1%/5%/10%, against 0.62/2.56/4.12 expected by chance; every p is at least 0.12. Mode 3 (leave-one-target-out logistic regression on frozen ESMC or ProtT5 embeddings; the other HER2 domain remains in the training set, so holding out one HER2 unit is related-epitope transfer, as the Mode 3 contract states): one of 12 comparisons has p < 0.05 before correction (ESMC pair features, Top-10%, 7/10, p = 0.031; 0.37 after Holm correction); the remaining eleven comparisons have p ≥ 0.12. We built no embedding features for D-SCRIPT, so it is reported for Mode 2 only. The Mode 2 library has 20,000 unique sequences: the 2,791 distinct Mode 1 sequences, 7,965 k-mutants of them made at the consensus design's variable positions, and 9,244 synthetic random sequences; none repeats a DARPinDB or Mode 1 sequence, so the 17,209 additions bring no new positives.

Cross-target labels (Q2). A sequence is labelled positive only for the target where it was measured and negative elsewhere as a task label, not as evidence of non-binding. We will use the term "task negative" throughout. To see how often this could matter, we compared every label-0 candidate in the Mode 1 libraries with all 179 DARPinDB binders. There are 37 exact matches to a binder of another target. Twenty-six belong to the HER2 DI/DIV shared pool described in Section 3.1. The other 11 entries, in six units, are two BCL-W binder sequences present in the random fill of those libraries. No label-0 candidate equals a binder of its own target. In the Modes 2 and 3 label matrix, one sequence is positive for two targets (HER2 DI and DIV). Unmeasured cross-target binders cannot be ruled out, so leave-one-target-out results are results on task labels. We will list the 37 matches in the appendix.

By 14 November we will upload a revised PDF with changes marked. We hope the revision addresses your concerns and merits a reassessment of the paper.

Dear Reviewer Hr8k,

Our revised PDF is now online, with changes marked in blue. In response to your review, the synthetic candidates are now called unlabelled synthetic candidates, with the HER2 binding check summarised; the decoy-composition sensitivity analysis (deletion and hidden-binder scenarios) is added as an appendix table; Modes 2 and 3 now have reference scores; the 37 cross-target label matches are listed in the appendix; and the limited precision of ten-unit aggregates is stated alongside the new null table.

We hope the revision addresses your concerns and look forward to your feedback. If you see anything else that should change, we will do our best to address it before the deadline.

Thank you for your questions.

Dear Reviewer Hr8k,

A gentle reminder that our revised PDF has been online since 13 November, with changes marked in blue. It responds to your questions on the synthetic candidates, the decoy-composition sensitivity analysis, and Modes 2 and 3.

The discussion period closes on 18 November (AoE), so time is getting short. If you have a moment, we would be grateful for your feedback and, if the revision addresses your concerns, an updated assessment. If anything else should change, a note in the next day would let us address it before the deadline.

Thank you for your time.

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

The paper releases DARPinDB (188 records, 37 targets, 179 binders, 121 with numeric KD, structures tiered with frozen chain maps) and DARPinBench, a ranking protocol on top of it. Mode 1 scores ten off-the-shelf methods on ten 500-member near-neighbor libraries. Modes 2 and 3 release sequences and labels only. The paper claims that no method reliably reaches the top 1%, and DockQ does not track library rank.

Critical strengths
  1. The paper raises an interesting and important task that is lack of attention. Ranking within a shared-scaffold library, where candidates differ by one or two substitutions and positives are rare, is not what SAbDab, PDBbind/SKEMPI or CASP/CAPRI/FoldBench measure. The paper is right that transferring success on generic heterodimer prediction to this setting is an assumption, not a result.

  2. Building the dataset is real work. Sequences, coordinates and binding readouts are genuinely scattered across PDB, SYNBIP and supplements, and joining them per-record with evidence class attached, structure tiered instead of flagged, and chain maps frozen separately, has not been done for this scaffold as far as I know.

  3. Running ten methods and freezing the matrix in advance is the right call, and the paper does not propose its own scorer.

  4. The pose-vs-rank result is the most convincing part. On EpoR both structure models reach almost the same DockQ (0.862 / 0.853) yet leave the same binder at rank 90 and rank 2; HER2_DIV shows the converse. This uses 13 crystal binders whose labels are not in question, so it does not depend on the aggregates I question below.

Critical weaknesses
  1. The negatives are not negatives. Only 9 of the 5,000 Mode 1 candidates were experimentally shown not to bind, all from one BCL-W SPR table. The 2,753 k-mutants are labeled 0 by construction. But they sit at median Hamming 0.013 from the nearest positive, about two substitutions, and those substitutions are at the variable positions the consensus scaffold is designed to tolerate. Many of the positives are sub-nanomolar. A two-residue mutant of such a binder can easily still bind, just weaker. So when a method ranks a k-mutant high, I cannot tell whether it failed or whether it found an unmeasured binder. Every failure rate in the paper contains this. The paper applies the opposite standard elsewhere. Section 3.1 keeps both HER2 records because calling the other epitope negative would create a false negative — correct, for 26 sequences. The same argument is not made for 2,753. Table S3’s unverified task negative = 0 is true by definition but hides this.

  2. No naive baseline, so the rankings may be sequence bias rather than interface understanding. There is no control without binding knowledge anywhere in the paper. A model can score sequences high because their composition resembles binders it has seen, not because it resolves the interface. Nothing here separates those two. Library construction makes this concrete. Random fill is 439/500 in JNK1 and BPP, 378/500 in VEGFR2, AcrB and CD40, 134/500 in EpoR. Random fill sits ~0.97 from the positives, k-mutants ~0.013, and positives sit inside the k-mutant cloud. So a scorer that only tells “real library member” from “random fill” lifts the positives for free. By my estimate (please check) such a scorer gets Top-10% ≈ 0.82 on JNK1 and BPP, ≈ 0.65 on VEGFR2/AcrB/CD40, ≈ 0.59 on EpoR, chance on the four units without fill — about 0.71 averaged, which beats nine of the ten methods. Table S11 points the same way: k-mutants are 74.4% of AF3’s top-25 and 70.0% of D-SCRIPT’s against a 55.1% base rate, and those are the two best methods. There is also no random-ordering null at all. From the per-unit n_pos I get roughly 0.06 / 0.26 / 0.41 at Top-1% / 5% / 10% (please check). Against that, both BioScore variants are below chance at Top-10%, several methods are inside noise, and AF3’s 0.80 is not separated from the null by more than the authors’ own intervals. Adding the null would make the main claim stronger, but the “sequence methods hit the front, structure methods recover later” story in Section 5.1 would not survive it.

  3. The dataset is too small to support the aggregates. 9 of 37 targets can anchor a unit. 66 positives total. Five of ten units have fewer than three positives. 9 experimental negatives. 13 complexes for DockQ. 130 of 188 records come from SYNBIP rather than primary literature. Top-k success is a count over ten units. Eleven possible values, each unit moves it by 0.1. The authors say themselves that interval width is set by sample size, not by the methods. The EF means are one unit each. From Figure 3c (please check): HER2_DIV is 17.00 of ProtT5’s 22.84, so 74% of its mean; BPP is 20.00 of AF3’s 38.00, so 53%. HER2_DIV is exactly the unit where the near-neighbor premise fails — it shares a pool with HER2_DI, mean Hamming 0.18, max 0.60 — so the sequence family’s whole advantage comes from a unit that breaks the construction. Section 6 explains why BPP’s 20.00 cannot be read across targets but does not do the same for HER2_DIV. Modes 2 and 3 do not help. 200,000 pairs is the same 66 positives over a bigger denominator, with no scores produced here.

Questions for authors
  1. Can you add a permutation null to Figure 3b and say which methods stay separated from it?
  2. Can you add a knowledge-free baseline that only separates k-mutants from random fill? If it lands near what I estimate, how do you restate the Top-10% results?
  3. Is there any published DARPin mutational scanning that would bound how often a single variable-site mutant keeps binding?
2 comments

Dear Reviewer DBgL,

Our revised PDF is now online, with changes marked in blue. Following your review, Section 5.1 is rewritten around each method's result against the random-ordering null (also added to Figure 3b); full and no-fill libraries are reported side by side; the member-versus-fill scorer and the neighbourhood-density baselines are in new baseline tables, with a note on which baselines read the whole library; the EF@5% contribution of HER2_DIV and BPP is tabulated; and the 107 SYNBIP-sourced records now have DOI/PMID provenance fields.

We hope the revision answers your concerns and look forward to your feedback. If anything else should be changed, we will do our best to address it before the deadline.

Thank you for the careful review.

Dear Reviewer DBgL,

A gentle reminder that our revised PDF has been online since 13 November, with changes marked in blue. The revision addresses the points in your review: the random-ordering null, the full and no-fill comparisons, and the new baseline tables.

The discussion period closes on 18 November (AoE), so time is getting short. If you have a moment, we would appreciate your feedback and, if the revision resolves your concerns, an updated assessment. If anything else needs changing, a note in the next day would let us address it before the deadline.

Thank you for your time.

Comments on the paper

2 comments
AuthorsOpenReview ↗

Summary of responses and planned revision

We thank the reviewers for their specific and careful reviews. Three concerns recur: the status of synthetic negatives, the lack of random and label-free controls, and unscored Modes 2 and 3.

1. Synthetic negatives (DBgL W1, Hr8k W1/Q1, UWL3 W1)

The 2,753 k-mutants are labelled 0 by construction, and some may bind. Constructed decoys are standard in screening benchmarks (DUD-E; Mysinger et al., 2012), and their construction can open shortcuts (Chen et al., 2019; Tran-Nguyen et al., 2020). DUD-E decoys are chosen to be topologically dissimilar from actives; ours differ by 1 to 3 substitutions from their parent sequences, mostly annotated binders, so binding is more plausible. We will therefore describe them as unlabelled synthetic candidates, not verified non-binders.

To test this directly, we measured binding experimentally in the wet lab on HER2 for 15 samples: two benchmark positives (A, B) and 13 high-scoring synthetic decoys. A and B gave apparent KD (1:1 fit) of about 4.96 and 5.43 nM. One decoy (C) showed about fivefold weaker binding, at about 23.8 nM; the other 12 showed no detectable binding. In this experiment the decoys either showed no detectable binding or bound more weakly than the positives. The benchmark asks whether annotated binders reach the front of a library, and these measurements support that criterion: for these candidates, ranking the decoys above A and B would put weaker or non-binding sequences first. The full data will appear in a separate work, and can be provided to the Area Chair in a confidential comment.

2. Random and label-free controls (DBgL W2/Q1/Q2, UWL3 Q6)

Exact random-ordering success at Top-1%/5%/10% is 0.063/0.257/0.414. Of 30 method-by-budget comparisons against this null, four have p < 0.05 before correction (ProtT5 Top-1%, ESMFold2 Top-5%, D-SCRIPT and AF3 Top-10%); none remains after Holm correction (smallest adjusted p = 0.125). A scorer that only ranks library members above random fill reaches 0.709 at Top-10%; AF3 (0.80) is the only method above it. With random fill removed, the ten methods succeed in 3 to 6 of 10 units at Top-10%, against 4.21 expected by chance.

A label-free baseline that counts, for each candidate, the other candidates within Hamming distance 3 places an annotated binder in the Top-1%, 5% and 10% in all ten units, with and without random fill. This follows from the design: positives with their own k-mutants are among the most connected sequences in their unit. At radius 6 it falls to 1.6/4.1/6.9 successful units with random fill and 1.3/2.5/3.9 without. It reads the whole candidate set, whereas each of the ten methods scores one (DARPin, target) pair at a time, so its success reflects library construction, not binding.

Affinity maturation enriches mutational variants of a parent binder, and selected DARPin binders can share sequence motifs. In an error-prone-PCR library derived from an anti-HER2 DARPin, 2% of unselected clones had ELISA signals similar to the parent clone's and 72% did so after four selection rounds (Houlihan et al., 2015); selected caspase-3 binders from ribosome display shared a conserved motif (Seeger et al., 2013). Hence the density baseline is relevant for libraries built from a binder and its variants.

3. Modes 2 and 3 (Hr8k W3/Q2, UWL3 W2, DBgL W3)

In Mode 2 (20,000 sequences shared across ten units), ESMC, ProtT5 and D-SCRIPT reach 1/2/2, 1/4/6 and 2/3/5 of 10 units at Top-1%/5%/10%, against 0.62/2.56/4.12 expected by chance; every p is at least 0.12. In Mode 3, leave-one-target-out logistic regression on frozen ESMC or ProtT5 embeddings (the other HER2 domain stays in training) has one nominal result among 12 comparisons (ESMC, Top-10%: 7/10, p = 0.031, 0.37 after Holm); the other eleven have p ≥ 0.12. D-SCRIPT is scored in Mode 2 only. The Mode 2 library holds the 2,791 distinct Mode 1 sequences plus 17,209 added sequences (7,965 k-mutants, 9,244 synthetic random) with no new positives.

4. Revision

By 14 November we will upload a revised PDF with changes marked. It will:

  • rewrite Section 5.1 around each method's result against the null, and add the null to Figure 3b;
  • report full and no-fill libraries side by side;
  • add a baseline table (random ordering, member-versus-fill, neighbourhood density at radius 3 and 6) and an appendix table of label-free baselines grouped by the information they use, marking which read the whole library;
  • replace "by design, not leakage" in Section 3.2 with a statement of this property and the library shape, and state the claim as retrieval of annotated binders;
  • add Modes 2 and 3 reference scores, a k-stratified figure and a robustness table;
  • add a timing note (MSA, BioScore, MEGADOCK), correct the hardware statement in the timing caption, and add a summary of the HER2 binding data;
  • add primary-literature DOI/PMID fields for the 107 SYNBIP-sourced records that carry only a SYNBIP identifier.

We hope these changes warrant a reassessment.

Dear Reviewers, Area Chair and Senior Area Chair,

A brief and polite reminder: the revised PDF and supplementary ZIP for Submission 26089 have been online since 13 November, with changes marked in blue, and a summary of changes is in our earlier comment.

As the discussion period closes on 18 November (AoE), time is getting short. We would be grateful for any feedback on the revision, and for an updated assessment if the changes address your concerns. If anything is still unclear or should be changed, please let us know soon so that we can address it before the deadline.

Thank you very much for your time and effort.

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

Related papers

Loading the map…

Discussion (0)

Sign in to comment.