acceptodds
Under review as a conference paper at ICLR 2027

Scaling works in biology if you use latents

Abstract

Scaling is a dominant paradigm in the field of artificial intelligence. Despite the advantages of scaling in computer vision and large language models, recent studies have shown that scaling models trained on genome and protein sequences plateau in performance when evaluating mutational effects in the zero-shot setting. This zero-shot setting compares the likelihood of a variant sequence and its wildtype sequence, under the assumption that likelihood is a proxy for general fitness. The likelihood is based solely on the probability that a sequence, , occurs in the distribution of the data on which the model is trained. This largely ignores the biological context of the variant, leading to poor prediction of mutational effects on phenotypes such as enzymatic catalytic activity. Here we show that simple supervised probes fitted to frozen model representations reveal scaling gains in phenotype prediction that zero-shot likelihood misses. By examining the latent space of protein and genome language models across different scales and deep mutational scanning benchmarks, we restore the gains that should be expected from scaling.

Primary area:
applications to physical sciences (physics, chemistry, biology, etc.)
Keywords:
fitness landscape, latent space, mutational effects, protein language models, genome language models, scaling laws

Reviews

Among:
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1234this paper, Top 15%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 3.00 over 3 reviews, above 85% of the others.
Reviewer_yJeeOpenReview ↗
Rating
3(+1)
Confidence
4
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

The paper asks whether biological language models are still learning more useful predictive information latently as they scale, even when zero-shot likelihood-based mutation/variant scoring (e.g., LLR) plateaus. They fit supervised probes to frozen embeddings from DNA, protein and RNA language models at different scales (ESM2, ProGen3, Evo2, and RiNALMo), and compare results on different tasks, in the different domains, primarily ProteinGym, FLAb2, NABench, growth and ADK. They check results in relation to mutation depth, fitness, regression - prediction beyond the training labels range, few shot learning, and transfer between tasks. They find that supervised probes generally outperforms zero-shot likelihood, and that larger models/scale often improve performance in several settings (moreso when using the supervised probes than in the 0 shot), although gains depend on model and domain. The authors conclude that these probes utilize scaling gains missed by likelihood scoring and can improve performance on predictions and assays/tasks.

Critical strengths
  1. Broad evaluation and comparisons across biological domains (dna/rna/prot), not just of models, is valuable and a useful reference point.
  2. Addresses a useful question of contrasting the approaches (and it’s saturation re scale) for variant scoring. Larger models saturating is known to practitioners, but is not necessarily established or citeable (Tables 6–7), and its non-intuitive to those from classic ml/nlp/dl (where bigger is typically better) .
  3. Useful generalization and transfer case studies: evaluating between tasks, predicting to out of distribution regression targets and the analysis on structure and sequence similar/dissimilar is interesting (although not that important to the overall paper I feel - but it is nice and inventive!) (e.g., Fig. 8).
Critical weaknesses
  1. The novel contribution needs clearer support. The introduction already acknowledges that supervised prediction from pretrained embeddings generally outperforms zero-shot likelihood, and this is what we’d expect in most ml tasks. The LLR/0 shot approaches are originally justified by generalizability, lack of bias, and perf (dataset bias/task specificness or species specificness is a separate kettle of fish. I can live with it not being investigated here, but it is relevant for future work).he interesting potential contribution is showing that larger models contain additional useful information that likelihood scoring misses. However, the aggregate results do not consistently establish this distinction. ESM2 largely plateaus at larger sizes under both approaches, while ProGen3 and Evo2 improve with scale under both (Tables 6–7). I do not expect every model family or biological task to improve with scale (give or take pretraining size, diversity, model size, model architecture/embedding scale or pretraining tasks). My concern is what new knowledge/novel claims the paper establishes beyond prior work. E.g., (as a non-binding example) the authors could distinguish the benefit of adding supervision from the additional benefit of model scale (e.g. embedding size or benefits from more pretraining) that likelihood scoring fails to capture, but that’s not necessarily the right question. Also, the conclusion that scaling is restored by this is stronger than the evidence presented, if only due to it not being the case in all the domains or models (e.g., RNA figure , although it not applying in all tasks/domains is fine by me and does not specifically affect my acceptance score).

  2. Hyperparameter and train/test splits need clarification re leakage. The paper sweeps layers, pooling windows, and normalization hyperparameters but does not clearly explain whether the final representation choices were selected independently of the test splits, doubly so given the many assays/tasks. Choosing configurations using test performance would bias the results in favour of the supervised approach. (I note that the best layers being final and 80% in those models is in alignment with other work, but them being searched for across many tasks and the other params is still a clear potential leak if there’s an overlap between train/test). It’s also unclear to me how train/test splits were done in the tasks, and if the authors did random splits, task defined splits (e.g. protein gym supervised splits), as random splits on many tasks is not enough given homologous families (that a supervised model especially can memorize, e..g close sequence homologs).

Questions for authors
  1. Main contribution and scaling Prior work and de facto best practices are that that supervised models from embeddings outperforms zero-shot likelihood/LLR in many cases and tasks (with the exceptions being the rule). What is your main new finding (about scaling) beyond this established result? As a non binding example (free to choose anything else), you could compare the per-assay changes in Spearman correlation across model sizes (give or take pretraining size) for the supervised probes and zero-shot, using the same assays and splits, and see In which cases do larger models improve supervised prediction when likelihood scoring does not? (and if it’s dependent on embedding size, model size, likelihood/perplexity, training size, memorization etc).

Tl;dr: Please clarify the main finding/claim/contribution here beyond “supervised learning does better than unsupervised/zero shot” - this is a must, and would move my score to accept.

  1. Hyperparameters. The paper sweeps layers, pooling windows, and normalization methods; but what was used to choose the configurations? Were these choices made using training/validation data only, independently of the final test folds (Across all assays)? Did you filter out (how? homology?) sequences appearing in any of the test sets, per domain and task/assay from this? If test scores informed configuration selection, please provide an independent evaluation of the affected results. E.g. naively choosing 80% or final layer by domain and mean pooling, defaults etc and comparing. Should report this. If its negligible params (e.g. just choosing one layer across all tasks and default pooling without tweaking), could also be enough to report on a few, while being clear about the leakage.
4 comments

Thank you for the feedback and questions! Our main claim is that scaling language models trained on biological sequence data improves model representations, which in turn improves downstream tasks such as mutational effect prediction when conditioned on the phenotype of interest. We will continue to clean up the writing on scaling monotonicity for the camera-ready paper.

Scaling evidence: We added Chinchilla parametric fits of test loss as a function of N total parameters and D tokens (Sec. 2.4, Fig. 4; App. A.9, Figs. 23, 24). With higher dimensionality more features can be represented, which we see as features such as ADK kcat emerging in larger PLMs. On ADK kcat the fitted phenotype direction reaches rho=0.51 against 0.43 for the likelihood direction, at a cosine similarity of 0.35, so the two directions are distinct (Fig. 2; Sec. 2.2). Fits for Evo2 and ProGen3 are still in queue and not yet in the revision. We also add further controls by training a ridge regression on the one-hot encoded representations of the sequence variants (pLM and gLM independent) and the supervisory labels. We see that the ridge regressions fit on pLM and gLM representations generally outperform the one-hot encoded version, especially for the modulo and contiguous fits, and that the probe improvement is not just from inclusion of supervisory labels, but rather, improvement in model representations with scale.

Non-binding example: We include the ADK enzyme's catalytic activity rates across its 30 stratified splits (Secs. 2.1, 3.1), plus a new final figure on general phenotype directions with all ProteinGym assays grouped by similar measurement type (abundance, growth, etc.).

Noncoding RNA: The linear probe's median across assays dips slightly at the largest size (0.324, 0.344, 0.338 at 33.5M, 148M, 651M) while its mean increases monotonically (0.329, 0.331, 0.339; Table 6). We also found that for RiNALMo we had reused one ridge penalty (lambda) selection (leave-one-out GCV) across the random, modulo and contiguous folds, which made the Spearman correlation on the position-held-out folds worse. We keep lambda selection matched per scheme elsewhere (App. A.5.2, A.5.5; Figs. 14 to 16); we missed it for RiNALMo because we added the fold schemes later, as modulo and contiguous splits were not originally in NABench, unlike ProteinGym. We are redoing this now.

Hyperparameters: We took the settings that were best for PTEN growth on ProteinGym's published random, modulo and contiguous schemes and used them for all probes on the other assays (Sec. 2.1; App. A.5.1, Figs. 10 to 13; App. A.5.4, Tables 4, 5). We could have varied this per assay, fold and scheme, but our point is that scaling improves biological model representations, and we did not want to bias the result by optimizing the probe for every setting. Only lambda is chosen by nested cross-validation on inner folds matched to the outer scheme (Eq. 12; App. A.5.5). Changing the normalization does not drastically alter any of the 36 probe-versus-likelihood comparisons, and we include a naive default baseline (last layer, mean pooling, no sweep). The normalization sweep is now mentioned in the main text and described more fully in App. A.5.4; we proceed with z-scoring across the training fold for all probes.

Training/Testing Splits: We use each benchmark's published partitions throughout, where ProteinGym's modulo and contiguous schemes hold out entire residue positions (App. A.2). This is now clearer in the main text, and we report results by split scheme as well as pooled, noting that on the contiguous scheme the probe ties the likelihood at 650M. We also extended both protocols to NABench, which did not come with those folds. For homology across duplicate or related proteins, we recomputed our significance tests over single-linkage 80% identity clusters (199 assays to 164 clusters); the median margin shifts by at most 0.025 and all conclusions hold.

Dependence on embedding size, model size, likelihood and training size: We like this idea and added the analysis across the 186 common ESM2 assays (App. A.7; Fig. 19). Assay phenotype accounts for the largest share of variance in probe rho (R2=0.23 to 0.33), ahead of MSA depth (0.11), taxon (0.10) and assay size (0.04). After controlling for the other factors, MSA depth correlates significantly with the zero-shot likelihood's accuracy (partial rho of +0.14 to +0.38) but not with the probe's accuracy, so lower homology coverage hurts zero-shot likelihoods much more than conditioned probes.

Reviewer_yJeeOpenReview ↗

Broken figure

Figure 4: your evo 2 subfigure is currently missing/broken in pdf

Reviewer_yJeeOpenReview ↗

Reply

Thanks for the reply and followup. The new analyses help, and I'm leaning towards raising my score from 2 to 3.

The supervised baselines address my concern that the results might just reflect adding labels.

I still have two concerns:

  1. Novelty. My original question wasn't only whether the gains come from supervision, but what's new compared to existing work (sorry if I wasn't clear enough). We know that supervised models often beat zero-shot, (e.g., ProGen3 and other works in dna and protein LLMs showed that scaling can help supervised prediction even when zero-shot gets worse or language modelling doesn't improve). Is the new finding that this also holds for simple probes on frozen representations, across different models and biological domains? If so, I think that's worth stating more clearly, rather than making broad claims about scaling laws in biology. I'd focus on making the actual contribution clearer.

  2. Possible leakage. Thanks for clarifying the hyperparameter selection. Using PTEN's test folds to choose the layer/pooling settings still worries me, even if those settings were then fixed for other assays. I'd suggest checking that the main conclusions hold without the tuning assays. I don't see this as a dealbreaker, but it does weaken the evaluation, as leakage applies to hyperparam etc settings; (I wouldn't change the score about this, just any takeaways).

Thank you for the follow ups! Regarding novelty and possible leakage:

Novelty: We show that scaling biological sequence models yields increasingly informative representations of biological phenotypes across multiple modalities, architectures, and model families. Beyond per-assay prediction we analyze fitness landscape geometry (Fig. 5, pg 6), the near-orthogonality of phenotype and likelihood directions (Fig. 7 pg 9), and phenotype directions that transfer to held-out assays and sharpen with scale (Fig. 8, pg 10, Appendix pg 36):

Comparison with literature:

While ProGen3 notes that latents become more informative with scale, they use iterative reasoning preference optimization (IRPO), which updates all model weights. In contrast, we keep weights frozen across ESM2, ProGen3, Evo2, and RiNALMo, and examine transferable phenotype vectors across unseen proteins (Fig. 8, p. 10).

Li et al. similarly use ridge regressions on ESM-1b and CARP embeddings. They conclude that fitness prediction does not always scale, as seen through a few tasks (AAV, GB1) that do not show improvements with increasing ESM-1b sizes. However, their model size ladders stop below 1B, whereas our divergence from the one-hot ridge regression is clearest at ESM2 3B to 15B. Also, they use full-sequence mean pooling, which dilutes single-residue substitions. Our pooling sweep (Fig. 10) confirms whole-chain pooling minimizes the latent advantage. Re-running their GB1 and subcellular localization benchmarks on ESM2 (8M–650M) confirms this: per-token for multiple mutational depths and mutant-site pooling for single mutations outperforms whole-chain pooling and recovers scaling on GB1, even if the improvements are monotonic.

Lin et al. show structural (TM-score) and perplexity gains up to ESM2-15B. Since the emergence of structural features with scale is pretty well established in Li et al. and Lin et al.,’s papers, we examine scaling in the context of mutational fitness and general multi-assay feature vectors (thermostability, growth, activity, abundance; Fig. 8, p. 10). This resolves Hou et al. (Nat. Comput. Sci., 2026), who show zero-shot likelihoods peak at moderate confidence and degrade at larger scales.

Prior gLM probing studies evaluate regulatory or variant-effect tasks without multi-scale sweeps within a single family or without systematic pooling/normalization sweeps (e.g., Datta et al., 2026). The closest work, Benegas & Czech's MarinDNA (Open Athena, Aug 2026) sweeps MarinDNA and Evo2. This is just a blog post and does not examine measured, quantifiable phenotypes.

Possible Leakage: Removing the hyperparameter-tuned assay changes the overall mean Spearman by only 0.005, indicating hyperparameter selection does not meaningfully bias our results (Appendix A5.2, pg 21). Moreover, we fit probes for a single layer depth per model family across all sizes (final layer for ESM2, ProGen3, RiNALMo; ~80% depth for Evo2 models) rather than selecting the best layer per model size, which may artificially favor larger models. Using ~75–80% layer depth for Evo2 is also independently supported by prior Evo2 sparse autoencoder interpretability studies (Brixi et al. 2026).

We are in the process of rewriting to include more related work and clarify our specific contributions. We also added the missing Evo2 subfigure that was still running at the time of the prior Friday revision. Please let us know if there is anything else you are curious about, and thank you again for the feedback!

Reviewer_16oBOpenReview ↗
Rating
3(+1)
Confidence
2
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

This paper investigates why he predictive performance of traditional zero-shot mutation effect prediction methods is gradually reaching a plateau. The authors argue that sequence likelihood ratio (LLR)-based prediction methods fail to adequately capture the specific biological functions of proteins. Therefore, they propose utilizing the latent representations of pre-trained models in combination with a small number of experimental labels to predict protein phenotypes such as stability, catalytic activity, and binding affinity. The authors evaluated their approach on four model categories and hundreds of biological experimental datasets, finding that Latent Probe is generally more accurate than traditional LLR predictions, and that prediction performance improves overall as model scale increases.

Critical strengths
  1. The research question is of significance: This work points out that the predictive performance of large biological models in predicting zero-shot mutation effects tends to plateau as the models scale up, and traditional evaluation methods based on sequence likelihood ratio may not fully reflect the biological functional information learned by the models. This perspective helps to reinterpret the scaling behavior of biological foundation models and provides valuable insights for evaluating large-scale pre-trained models.
  2. The experiments are comprehensive: The authors conducted systematic validation across four model families and hundreds of biological experimental datasets, covering various phenotypes. The experiments compared predictive performance across different model scales and analyzed mutation depth, functional landscape reconstruction, and cross-protein generalization capabilities.
Critical weaknesses
  1. Limited Novelty and supervised learning baseline are required: The core method involves using standard Ridge Regression or MLP to perform supervised learning on the latent space representations of pre-trained models, which is a widely adopted approach. More importantly, the authors primarily compare a “Probe” trained using real phenotypic labels with a completely zero-shot LLR, and the supervision conditions for the two are not consistent. Therefore, the existing experiments make it difficult to distinguish whether the performance improvement stems from better pre-trained representations or from additional supervisory information. More comprehensive supervised learning baselines are required to substantiate this claim.
  2. More sufficient evidence and experiments are required: Although the experiments show that increasing model size generally improves predictive performance, the improvement is not always significant or monotonic. Besides, in the labeling efficiency experiments, the authors screened the training data using the true phenotypic values of candidate samples, which may have led to an overestimation of performance on small datasets.
Questions for authors
  1. The fairness of supervised learning baselines: The paper primarily compares Latent Probe (trained using true phenotypic labels) with Zero-shot LLR. Did the authors consider conducting a comparison under the same supervision, such as training a supervised regression model using LLR scores or simple sequence features? How can they demonstrate that the performance improvement stems primarily from better pre-trained representations rather than additional supervised information?
  2. The reliability of the scaling conclusions: Some models show very limited performance improvements when scaled up. Did the authors conduct statistical significance tests? How can we determine that these minor improvements are sufficient to support the paper’s core conclusions regarding scaling?
2 comments

Thank you for your comments! In Figure 2 (page 3; discussed in Section 2.2; Appendix A.6, page 26), we train a supervised ridge regression model on the last hidden state of ESM2-3B using the ESM2-3B zero-shot likelihood (LLR) scores as the training target for 3 assays (ADK, Tsuboyama G, and PTEN growth). It is a good idea to have matched supervised comparisons across more assays, which we present in Appendix A.4 (pages 17 to 18).

In these extended comparisons added to the appendix A.4, we do the following additional evaluations:

  1. Training ridge regression directly on the scalar LLR score results in similar trends as LLR, with larger models having a lower Spearman correlation.

  2. To compare against supervision without PLM representations, we also trained a matched ridge regression model on one-hot mutation encodings, rather than language model representations.

The PLM probe's advantage over it grows monotonically with scale across all three split schemes (+0.126 to +0.303 on modulo, +0.029 to +0.223 on contiguous, and -0.004 to +0.078 on random). While one-hot encoding performs well on random splits (0.704) due to position overlap, it drops to 0.254 and 0.257 on the position-held-out modulo and contiguous splits, which is where the PLM representations provide the largest gain.

Following your suggestion, we also added statistical significance tests across all comparisons, paired at the assay/domain/split level rather than by individual variants (Tables 6 and 7, pages 27 to 28). For each comparison, we report the median margin, 95% bootstrap confidence interval (10,000 resamples), two-sided Wilcoxon signed-rank p-value, win rate, and Benjamini-Hochberg adjusted p-value. Out of 316 test cells across four model families, three substrates, and both probe types, 285 remain significant at =0.05 after adjustment. We will add further detail in the appendixes as well.

Finally, we redid the label efficiency analysis using uniform random sampling without screening by the true phenotypic experimental measurements (Section 3.3, pages 8 to 9; Appendix A.12, pages 39). Every sampled variant is counted toward the experimental budget n, and we report budgets across the six assays carrying all three ESM2 checkpoints (35M, 150M, and 650M) rather than taking a median across the model ladder. We also see that larger models require fewer labels to reach the same accuracy, dropping from a median of 768 variants at 35M to 256 at 150M and 650M and never increasing across any of the six assays. Under position-held-out grouped folds, four of the six assays allow for label reduction to 256 to 1024 variants (4- to 27-fold reduction).

Thanks the reviewers for the reply. My concerns have been answered. I would like to raise my score to weak accept.

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

This paper fits ridge-regression and MLP head to latent representations for phenotype prediction.

Critical strengths
  1. The paper distinguishes the information available in pretrained representations from what a particular readout captures. This is practically relevant, and the probing methods are simple.
  2. The evaluation spans four model families and diverse phenotypes, with over 300 assays in some settings. For example, ProGen3's mean linear-probe Spearman correlation increases from 0.514 at 112M to 0.618 at 3B (Table 6).
  3. The authors examine layers, pooling, normalization, and multiple split schemes. Training-fold standardization, inner-fold ridge regularization selection, and training-only MLP early stopping are useful controls. Positional and sequence-similarity limitations are acknowledged.
Critical weaknesses
  • The measurement-efficiency analysis utilises information from a larger pool of labels to select fitting samples; therefore, the reported n does not correspond to the number of measurements queried in a prospective experiment.

  • The results show scale-dependent gains, but these are insufficient to establish a universal quantitative scaling law: ESM2 tends to plateau around 650M–3B, and the median of RiNALMo may even decrease.

  • Transfer is strongest between closely related proteins, even including nearly identical pairs, and therefore cannot yet demonstrate extensive transfer to distantly related proteins or previously unseen families. Reporting should include alignment coverage, full-length sequences, variant-level overlaps, and deduplication status, along with assessments for homologous clusters or family holdouts. Stratification by the number of mutations does not validate extrapolation from low-order to high-order mutations; the composition of training depth should be reported, and a clear definition from low-order to high-order must be established.

If the authors would like to address these weaknesses, I am willing to improve my score.

Questions for authors
  1. Does Table 1's label-efficiency advantage persist under random or sequence-based selection without access to unqueried fitness labels, counting every measurement toward the budget?
  2. Under matched label budgets and tuning protocols, do the probes outperform simple supervised baselines, and do larger-model gains persist with matched probe capacity and paired confidence intervals?
4 comments

Thank you for the thoughtful comments! In terms of label efficiency, we redid the efficiency test with uniform random sampling and label-free sequence-diversity sampling (Sec. 3.3; App. A.12). On random splits at 650M, 128 to 512 labels are enough to match the zero-shot likelihood, a 9x to 27x saving over the full dataset. On folds that hold out whole positions, four of six assays still show a 4x to 27x reduction compared to the total dataset.

In terms of the other controls for the probes, we added a ridge regression on one-hot encoded features with no language model involved (Sec. 2; App. A.4, Fig. 9; matched-budget controls in App. A.12). We use the same labels, the same training/testing folds as the latent-based probe, the difference is just how sequences are represented. The one-hot ridge regression is comparable to the latent-based probe only on random splits, where a position can appear in both training and test data. Once whole positions are held out, the one-hot ridge does much worse than the latent-based probes. This is because one-hot features carry no information about a position never seen in training, while model embeddings have a better representation of this. Furthermore, the latent-based probe's advantage over the one-hot encoded ridge regression increases with scale, from +0.126 to +0.303 on modulo splits and from +0.029 to +0.223 on contiguous splits.

To rule out that the trend is just the extra parameters, we are adding a control that reduces every checkpoint's embeddings to 320 dimensions before fitting, giving every probe the same size. We are also adding bootstrap 95% intervals, resampling assays, on the per-assay gap between probe and zero-shot and on the change from one checkpoint to the next.

On RiNALMo, the linear probe's mean rises (0.329, 0.331, 0.339), while the median seems to decrease. We found a mistake on our side that may cause the linear probe medians to be lower: for RiNALMo we reused a single regularization value based on the random folds that are part of that benchmark, which made the held-out-position modulo and contiguous schemes that we created for this paper worse than they should be. We are refitting with the penalty chosen per scheme, as we already did for the other models. On random folds the median rises monotonically (0.670, 0.671, 0.681), so we expect that we should see the increase as well for the other schemes once refit.

Regarding cross-protein transfer, we agree, and we will add a per-pair audit of alignment coverage, chain lengths and length ratio, variant overlap and deduplication. It confirms your concern that the homolog tier is largely re-scans of the same positions: all 13 within-cluster pairs share at least half of their measured variants. We will limit that Sec. 4 pooling claim to close homologs and give the identity range. However, we have since added a new result about broader generalization. Figure 8 averages the directions fit on separate ProteinGym assays for the same phenotype and tests them on whole held-out assays. These are unrelated proteins rather than homologs, and the averaged direction still reaches a Spearman correlation of 0.35 to 0.51 for thermostability, growth, abundance and activity. Binding is the exception, with a much lower Spearman correlation of 0.11, likely because it also depends on the specific antigen and not just binder sequences.

The training/testing splits for multiple mutational depths are random, as provided in the ProteinGym benchmark. The Spearman correlations from these assays are part of the kernel density plots, implicitly, so we have moved it to the appendix. The appendix version of the mutational depth results include more counterfactuals and controls, like the once mentioned earlier. We instead added a section on Chinchilla scaling law fits to further reinforce this paper's scaling contributions, although the nats per token jobs are still running.

We added an ethics statement and are glad to add anything else that would be helpful for the paper!

Reviewer_ryTMOpenReview ↗

Response

The author has addressed my questions regarding the technical details.

Reviewer_ryTMOpenReview ↗

Response

The authors have addressed my questions about the technical details.

Thank you for responding! We are glad the technical details are clearer now. Beyond the technical clarifications, we also included some new experiments in the revision to cover your other initial feedback. Do those resolve your remaining concerns, or is there anything else you'd like to see added to warrant an improved paper?

Comments on the paper

1 comment

Hi reviewers,

Thank you for your reviewing service. The authors have provided fairly extensive rebuttals. Please confirm that you have read them, state which of your concerns are or are not addressed, and whether that changes your recommendations.

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

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