acceptodds
Under review as a conference paper at ICLR 2027

Rethinking Heterogeneous LLM Merging: A Weighted Model Averaging Perspective

Abstract

Can large language models with substantially different parameter spaces be merged by direct weighted averaging, without training or semantic alignment? Existing heterogeneous fusion methods typically introduce distillation, adapters, learned latent spaces, routing, or feature alignment, leaving open whether a simpler recipe can work for genuinely different billion-parameter checkpoints. We revisit this counterintuitive question through training-free dimensional adaptation followed by ratio-controlled interpolation. In intersection-style merging, we truncate the larger model into the smaller parameter space; in union-style merging, we expand the smaller model into the larger parameter space (Figure 1). Across Qwen-family model pairs and benchmarks covering mathematical reasoning, code generation, language understanding, commonsense reasoning, knowledge, and instruction following, deterministic expansion largely preserves the source model function, and small-ratio interpolation can improve over strong source checkpoints by transferring complementary capabilities. However, near-balanced interpolation often collapses, and task-level results reveal a seesaw effect in which gains on some capabilities coexist with regressions on others. These results show that simple parameter averaging, when paired with lightweight dimensional adaptation and carefully controlled ratios, is a surprisingly strong baseline for heterogeneous LLM merging, suggesting that the limits of direct weighted fusion may also bound what more complex heterogeneous merging methods can achieve at scale.

Primary area:
foundation or frontier models, including LLMs
Keywords:
Heterogeneous LLM Merging, Weighted Model Averaging, Training-Free Fusion, Dimensional Adaptation, Model Interpolation

Reviews

Among:
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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_z8bwOpenReview ↗
Rating
3
Confidence
2
Informativeness
2
Presentation
3
Soundness
2
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Paper summary

This paper investigates training-free heterogeneous LLM merging through dimensional adaptation and weighted model averaging. The proposed approach uses truncation or expansion to align parameter dimensions before interpolation. Experiments across Qwen, Llama, and Gemma model families examine merging performance and the effects of interpolation ratios on different tasks.

Critical strengths
  1. The paper addresses a clear research question with straightforward presentation. Dimensional adaptation followed by weighted interpolation provides a simple and useful baseline for studying heterogeneous model merging.
  2. The evaluation covers multiple model families and 16 benchmarks, including fixed-ratio results, perturbation controls, and comparisons with other merging methods. The results demonstrate that simple weight interpolation can improve performance for certain model pairs.
Critical weaknesses
  1. The dependence on interpolation ratios deserves further investigation. The Potential values emphasized in the main tables are obtained by selecting the best interpolation ratio separately for each task, rather than evaluating a single merged checkpoint. Although Appendix C reports fixed-ratio results, including configurations that achieve genuine improvements, their gains are generally smaller than Potential. Selecting a fixed ratio using held-out validation data and evaluating its test performance would help clarify the improvements achievable in practice.

  2. The architectural compatibility requirements could be clarified further. Although the experiments cover Qwen, Llama, and Gemma, merging is primarily performed between models of different scales within the same family. Appendix D also acknowledges that dimensional adaptation relies on architectural compatibility. Clarifying the specific requirements of Truncate and Expand, and discussing their applicability to other heterogeneous architectures, would better establish the scope of the approach.

Questions for authors
  1. If a fixed interpolation ratio is selected using held-out validation data, how does its test performance compare with the reported Potential values?
  2. What specific architectural compatibility conditions are required by Truncate and Expand, and how do these conditions affect the applicability of the approach?
2 comments
AuthorsOpenReview ↗

From Oracle Potential to Practical Gains: Validation-Based Selection and Cross-Family Compatibility

Response to Reviewer z8bw: Validation-Based Ratio Selection and Architectural Compatibility

We thank the reviewer for these questions. We conducted held-out validation experiments, completed a cross-family evaluation on all 16 benchmarks, and will clarify the requirements of Truncate and Expand.

R3.1. Performance after validation-based ratio selection

We split each task once into 30% validation and 70% test data. All ratios used the same split, and test data were never used for selection. We selected one global ratio using the unweighted mean over the 16 validation tasks.

Global ratio μ\mu0.010.020.030.040.05
Validation mean (%)55.7556.2555.7054.9654.69

Validation selected μ=0.02\mu=0.02. We evaluated this single checkpoint on held-out test data and also tested task-aware selection, where each task uses only its validation data to select a checkpoint.

Selection ruleEvaluation dataMerged result (%)Corresponding 3B baseline (%)Gain
One global ratio selected on validation70% held-out test set54.9853.88+1.10
One ratio per task selected on validation70% held-out test set55.9753.88+2.09
Best fixed checkpoint reported in the paperFull evaluation set55.5454.59+0.95
Potential reported in the paperFull evaluation set57.1654.59+2.57

The validation-selected global checkpoint gains +1.10, comparable to the paper's best fixed-checkpoint gain of +0.95. Task-wise validation selection gains +2.09, approaching the +2.57 oracle gain represented by Potential. Because the new results use the 70% test split while the paper uses the full set, we compare gains over the corresponding 3B baselines, not absolute scores across sets.

Global validation selection produces one deployable checkpoint; task-wise validation selection uses task identity but not test performance; Potential uses test performance and is therefore an oracle upper bound. We will clarify this distinction.

R3.2. Compatibility requirements and cross-family applicability

Our compatibility rule is selective, recipient-anchored parameter injection. One model is the donor and the other is the recipient. We apply three rules:

  1. Donor-only components are not injected.
  2. Components present in both models are injected only when their module types, architectural positions, tensor-dimension mappings, and numerical parameterizations are compatible.
  3. Recipient-only components retain their original recipient values.

For Truncate, the donor tensor must be no smaller along the adapted dimensions and reducible to the recipient shape along predefined architectural axes. For Expand, the donor tensor is injected into the mapped part of the recipient tensor, while the remainder retains recipient values. Neither operation uses semantic alignment or learned matching.

Shape compatibility alone is insufficient. Components with incompatible parameterizations or scales are excluded. For example, Gemma and Qwen RMSNorm parameters have markedly different scales, so we retain the recipient's normalization parameters.

To test whether the method is restricted to within-family merging, we completed all 16 original benchmarks for a 2×22\times2 donor-recipient design.

Donor →\rightarrow RecipientRecipient baseline (%)Best fixed ratioMerged mean (%)Gain
Qwen2.5-32B →\rightarrow Qwen2.5-3B54.590.0155.54+0.95
Llama-3.3-70B-Instruct →\rightarrow Qwen2.5-3B54.240.0254.90+0.66
Qwen2.5-32B →\rightarrow Llama-3.2-3B42.610.0142.24-0.37
Llama-3.3-70B-Instruct →\rightarrow Llama-3.2-3B42.610.0142.25-0.36

The positive Llama-to-Qwen result shows that same-family membership is not necessary for positive transfer; the absence of an average Llama-to-Llama gain shows that it is not sufficient. Cross-family merging is applicable when enough components admit the required mappings; incompatible components are skipped.

Compatibility makes injection well-defined but does not guarantee improvement. With few compatible components, fewer donor parameters are transferred. Outcomes also depend on the recipient, tasks, and ratio. Gains are more consistent with Qwen2.5-3B as recipient here, but the tested pairs do not establish the cause. We will state these requirements and limitations explicitly.

AuthorsOpenReview ↗

Additional cross-family result: Llama-3.3-70B-Instruct Qwen2.5-3B

Thank you again for highlighting practical ratio selection and cross-family applicability. In addition to the fixed-ratio results in our rebuttal, we completed the task-wise IM Potential sweep for Llama-3.3-70B-Instruct →\rightarrow Qwen2.5-3B. The table reports the corresponding Qwen2.5-3B baseline from the same evaluation:

Dataset3B baselineCross-family IM Potential
GSM8K65.6665.0
MATH-50038.4038.6
HumanEval+43.9037.2
MBPP+58.9960.6
IFEval40.4141.1
BoolQ70.8074.3
COPA78.0081.0
MNLI45.9849.4
PIQA75.7975.9
QNLI52.8661.2
RTE64.2681.2
WinoGrande63.3864.2
ARC34.4239.0
HellaSwag50.9467.6
MMLU44.9645.3
BBH44.6346.9
Average54.5958.0

The cross-family Potential improves the matched average by 3.41 points and improves 14 of 16 tasks. We emphasize that this is a task-wise oracle envelope, not a single deployable checkpoint; its purpose is to quantify cross-family headroom. The positive fixed-ratio result already reported in our rebuttal separately shows that cross-family transfer is attainable with a single checkpoint.

Together with the validation-selected and compatibility results in our rebuttal, this evidence shows that same-family membership is not necessary for positive transfer, while architectural compatibility alone does not guarantee it. If these results address your concerns, we would appreciate an updated assessment; otherwise, we would be grateful for any remaining question about the method's scope.

Reviewer_CMUDOpenReview ↗
Rating
1
Confidence
3
Informativeness
1
Presentation
2
Soundness
2
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Paper summary

This paper studies how to use model merging with different sizes. The authors propose two approaches: intersection-style merging where the larger model is truncated and then merged into the smaller parameter space, and union-style merging where the smaller model parameter space is expanded and merged into the larger model's parameter space. The paper finds that these two simple model merging approaches have potentially higher performance than the base model by transferring complementary capabilities, which serves as an important baseline for approaches that combine heterogeneous LLMs. They also find that near-balanced merging leads to collapse while the small or larger merge coefficient (≤0.05\le 0.05 or ≥0.95\ge 0.95) works.

Critical strengths
  1. The presentation in the main paper is clear to me. Figure 2 clearly illustrates how the intersection-style merging and union-style merging work.

  2. The experiment is comprehensive: The authors use different model families (Llama, Qwen, Gemma) and different sizes ranging from small models (2-3B) to large models (32B).

Critical weaknesses
  1. First, in Table 4-6, the "potential" result is the best result for each benchmark across the merging coefficients. Hence, it is not clear whether this improvement is due to the true benefit of model merging or the randomness in the evaluation on different models. Actually, in Appendix C, if the merging coefficient is fixed, none of the merging coefficients can lead to clearly better performance over baselines.

  2. Moreover, the ablation study in A.1 (studying the comparison of just merging noise) only picks some benchmarks where the performance of the model merging is higher than the baseline. It is not a fair comparison and does not prove that this model merging approach outperforms merging with noise. Also, it does not rule out the possibility that the improvements reported in this paper are due to randomness. Also, how the noise is constructed in the ablation study is not clearly stated in Section A.1.

Given these two points, I am not convinced that there is a clear improvement for intersection-style merging and union-style merging over the base model.

Questions for authors
  1. There is no carefully designed truncation in the intersection-style approach. Is it possible to find a way to keep the core capabilities during truncation and then merge with the smaller model?

  2. Can the author show the complete results including more benchmarks, in the ablation studies in Section A.1?

  3. Does the failure of the nearly balanced merging coefficient imply that the truncated or expanded models are just noise?

3 comments
AuthorsOpenReview ↗

Clarifying Fixed-Checkpoint Gains, Full Noise Controls, and Dimensional Adaptation

We thank the reviewer for recognizing the clarity of Figure 2 and the breadth of our experiments. We address each concern below.

1. Potential versus fixed checkpoints.

We agree that Potential is not one deployable checkpoint: it is the per-task best envelope over a fixed ratio grid. Appendix C separately reports every fixed-ratio checkpoint and its 16-task mean.

However, the claim that no fixed coefficient improves the baseline is inconsistent with the reported results. For Qwen2.5-3B intersection-style merging, the baseline is 54.59, while four single checkpoints obtain 55.54, 55.51, 55.14, and 55.23 at μ=0.01,0.02,0.03,0.04\mu=0.01,0.02,0.03,0.04. For Qwen3-14B/32B union-style merging, the stronger source scores 74.74, while the single λ=0.98\lambda=0.98 checkpoint reaches 76.10. These are individual checkpoints, not task-wise oracle combinations. Our limited claim is that a small fixed injection can improve the average without training or learned alignment—not that every pair, task, or ratio improves.

2. Complete noise controls (R1.2).

We agree that the original seven-setting diagnostic was insufficient as a benchmark-wide comparison. We therefore evaluated all 16 benchmarks at all five ratios using two Gaussian controls. Both use the same ratio grid and selection budget as donor injection. The stricter control additionally matches the injected parameter support and per-tensor perturbation norm. For each injected tensor,

\hat\epsilon_l=\epsilon_l\frac{\|\Delta_l\|_F}{\|\epsilon_l\|_F},\quad \theta_l^{\mathrm{noise}}(\alpha)=\theta_l^{\mathrm{recipient}}+\alpha\hat\epsilon_l.$$ | 16-task mean | $0.01$ | $0.02$ | $0.03$ | $0.04$ | $0.05$ | |---|---:|---:|---:|---:|---:| | 3B baseline | 54.59 | 54.59 | 54.59 | 54.59 | 54.59 | | Actual donor injection | **55.54** | **55.51** | **55.14** | **55.23** | 54.59 | | Ordinary Gaussian | 54.42 | 54.31 | 54.41 | 53.98 | 54.11 | | Norm-matched Gaussian | 54.65 | 54.56 | 54.15 | 53.55 | 53.03 | The ordinary control never exceeds the baseline; the norm-matched control gains at most **+0.06**, whereas donor injection gains **+0.95**. Thus, expansion, grid search, generic noise, and perturbation magnitude are not sufficient explanations. The result is consistent with the structured donor direction carrying model-specific information, but we will revise “complementary capability transfer” from a mechanism claim to a hypothesis. **3. Why Truncate is not designed to preserve the full large-model function (R1.1).** Preserving all capabilities after reducing a large model to a smaller architecture is a different objective. Truncate is a deterministic, training-free projection: compatible tensors are copied, oversized tensors are sliced, and layers beyond the target depth are removed. Because parameters are discarded, **Truncate is inherently lossy**, and we do not claim that the projected checkpoint independently preserves the large model's function. This is asymmetric with Expand. Expansion can insert existing coordinates into a larger space, zero-initialize new attention/MLP branches, use neutral normalization values, and initialize added blocks as residual identities. Preserving a large model under Truncate would instead require learned compression or distillation. Our question is whether a structured truncated checkpoint can transfer useful information as a small perturbation of a working recipient. The fixed-checkpoint results above show that it can. **4. Balanced-ratio collapse does not imply random noise (R1.3).** Direct averaging gives substantial weight to two heterogeneous parameterizations without learned alignment and can disrupt both; this is why we interpolate near a working source. Coarse-ratio collapse identifies the operating boundary of direct averaging, not equivalence to noise. Expansion-only results further separate adaptation from noise: | Source $\rightarrow$ expanded architecture | Source mean | Expanded-only | Change | |---|---:|---:|---:| | Qwen2.5-14B $\rightarrow$ Qwen2.5-32B | 70.44 | 70.34 | **-0.10** | | Qwen3-4B-Thinking $\rightarrow$ Qwen3-8B | 62.71 | 62.71 | **<0.01** | | Qwen3-14B $\rightarrow$ Qwen3-32B | 74.27 | 74.50 | **+0.23** | Expansion therefore approximately preserves aggregate behavior. For Truncate, we make no independent-function claim; it is a structured checkpoint-derived perturbation used at small weight. Four neighboring fixed ratios improve the 16-task mean, while neither Gaussian control reproduces this pattern. We will add the complete controls and clarify these claim boundaries in the revision.
AuthorsOpenReview ↗

Follow-up on the additional controls

Thank you again for your review. Our rebuttal provides the complete 16-task, five-ratio noise controls requested in R1.2, including a stricter Gaussian control matched to the injected parameter support and per-tensor perturbation norm. It also clarifies that the reported fixed-ratio improvements come from individual checkpoints rather than the task-wise Potential envelope. Under the same evaluation, donor injection improves the mean by +0.95, whereas the best matched-noise result improves it by only +0.06. We therefore limit our conclusion to evidence against generic random perturbation as a sufficient explanation, without claiming that the control proves a specific transfer mechanism.

Regarding R1.1, Truncate and Expand are inherently asymmetric. Expand can approximately preserve the source function by placing existing parameters into a larger architecture and assigning neutral values to the added coordinates. Truncate necessarily removes parameters or coordinates and is therefore a lossy operation; under our deterministic, training-free setting, it cannot generally guarantee preservation of the source model's function or performance. Developing a capability-preserving compression method would require additional machinery such as learned projections, retraining, or importance-aware parameter selection. This is a valuable separate direction, but it is not the question studied here: our goal is to establish a simple training-free baseline for whether limited injection from a dimensionally adapted donor can benefit the recipient.

We would appreciate knowing whether the additional controls and clarifications address your concerns. If any specific issue remains unresolved, we would be glad to address it directly.

Thank you for the detailed rebuttal. However, I remain unconvinced that the improvement of less than 1 point (54.59 vs 55.54) provides clear evidence of improvement, and the difference between the donor injection and the best matched-noise result is also small. Hence, I maintain my score.

Reviewer_azB8OpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

This paper investigates whether LLMs of different sizes and structural compatibility can be directly merged without training or semantic alignment. The proposed method first truncates the larger model or expands the smaller model, and then performs small-scale weight interpolation. On each model, some proportions can improve performance, but near-equilibrium interpolation often leads to performance collapse.

Critical strengths

(1) The method is simple and low-cost, providing a comparable baseline for merging heterogeneous models; the appendix also reports the actual benefits of fixed proportions.

(2) The experiments retain results showing large-scale interpolation failures, uneven cross-family benefits, and better results from some baselines, providing some explanation of the method's applicability.

Critical weaknesses

(1) The main table highlights the potential for selecting the optimal proportion on a task-by-task basis, but it does not correspond to a single model. For example, the mean of Qwen2.5-3B increases from 54.59 to 55.54 with the optimal fixed proportion, while the potential reaches 57.16. While the paper explains this distinction, it still lacks results from selecting a proportion on the validation set and then fixing the test, as well as an uncertainty analysis of the main gains.

(2) Evidence to interpret the gains as "complementary capabilities" is insufficient. The complete task baseline of the expanded but not merged models is missing, and the noisy control does not adequately explain the construction and matching methods, making it difficult to distinguish the effects of capability transfer, dimensional adjustment, and general perturbations.

Questions for authors

(1) After selecting a proportion on the validation set, how much of the test set gain is retained?

(2) How does the expanded but not merged model perform, and does the noisy control use the same selection budget and perturbation scale?

(3) Can the expansion configuration of each model pair be clearly defined, and the differences in output before and after expansion be examined?

3 comments
AuthorsOpenReview ↗

Validation-Based Selection, Expansion Controls, and Matched Perturbation Analysis

From Oracle Gains to Controlled Evidence: Response to Reviewer azB8

We thank the reviewer for identifying the need to separate validation-based selection, expansion effects, and generic perturbations. We added the requested controls and will revise “complementary capability transfer” from a mechanism claim to a hypothesis consistent with the evidence.

R2.1. How much gain remains after validation-based selection?

We split every task once into 30% validation and 70% test data. All ratios used the same split, and test data were never used for selection. The unweighted mean over the 16 validation tasks selected one global ratio, μ=0.02\mu=0.02 (56.25%). We also evaluated task-wise validation selection.

Selection ruleEvaluation dataResult3B baselineGain
One global ratio selected on validation70% held-out test54.9853.88+1.10
One ratio per task selected on validation70% held-out test55.9753.88+2.09
Best fixed checkpoint in the paperFull set55.5454.59+0.95
Potential in the paperFull set57.1654.59+2.57

Because the new and paper results use different evaluation subsets, we compare gains over their corresponding baselines, not absolute scores across sets. Global selection produces one deployable checkpoint; task-wise selection uses task identity but not test performance; Potential uses test performance and is therefore an oracle upper bound.

For uncertainty across tasks, a paired task-level bootstrap over the 16 score differences (200,000 resamples) gives +0.95 [95% CI: +0.25, +1.76] for the paper's best fixed checkpoint and +1.10 [+0.07, +2.28] for the validation-selected checkpoint. We therefore claim an average improvement over this suite, not uniform gains across all tasks.

R2.2. Expansion-only and Gaussian controls

We evaluated every expanded checkpoint before merging:

Source →\rightarrow expanded architectureSource meanExpanded-only meanChange
Qwen2.5-14B →\rightarrow Qwen2.5-32B70.4470.34-0.10
Qwen3-4B-Thinking →\rightarrow Qwen3-8B62.7162.71<0.01
Qwen3-14B →\rightarrow Qwen3-32B74.2774.50+0.23

Thus, expansion alone approximately preserves aggregate behavior and does not explain the main merging gains.

Both Gaussian controls use the same five-ratio grid and selection budget as donor injection. The ordinary control uses θ+αϵ\theta+\alpha\epsilon, ϵ∼N(0,I)\epsilon\sim\mathcal N(0,I). The stricter control additionally matches the injected parameter support and each tensor's perturbation norm:

\hat\epsilon_l=\epsilon_l\frac{\|\Delta_l\|_F}{\|\epsilon_l\|_F},\qquad \theta_l^{\mathrm{noise}}(\alpha)=\theta_l^{\mathrm{recipient}}+\alpha\hat\epsilon_l.$$ | Setting | Best 16-task mean | Gain over 3B (54.59) | |---|---:|---:| | Ordinary Gaussian | 54.42 | **-0.17** | | Norm-matched Gaussian | 54.65 | **+0.06** | | Actual donor injection | **55.54** | **+0.95** | Neither random control reproduces the donor-injection gain. This rules out expansion alone, search budget, generic noise, and perturbation norm as sufficient explanations. It is consistent with the structured donor direction carrying model-specific information, but does not by itself prove a specific capability-transfer mechanism. ## R2.3. Pair-specific expansion configurations and output changes | Source $\rightarrow$ Target | Hidden | MLP | Layers | Q heads | KV heads | Head dim | |---|---:|---:|---:|---:|---:|---:| | Qwen2.5-14B $\rightarrow$ Qwen2.5-32B | 5120→5120 | 13824→27648 | 48→64 | 40→40 | 8→8 | 128→128 | | Qwen3-4B-Thinking $\rightarrow$ Qwen3-8B | 2560→4096 | 9728→12288 | 36→36 | 32→32 | 8→8 | 128→128 | | Qwen3-14B $\rightarrow$ Qwen3-32B | 5120→5120 | 17408→25600 | 40→64 | 40→64 | 8→8 | 128→128 | Existing hidden, attention-head, and MLP coordinates are placed through deterministic slot maps. New linear coordinates are zero-filled; added attention/MLP branches are zero-initialized; added layers are residual identity blocks; and new normalization scales receive neutral initialization. No training or learned alignment is used. | Source $\rightarrow$ expanded architecture | Mean change | Mean absolute task change | Maximum task change | |---|---:|---:|---:| | Qwen2.5-14B $\rightarrow$ Qwen2.5-32B | **-0.10** | 0.40 | 1.77 | | Qwen3-4B-Thinking $\rightarrow$ Qwen3-8B | **<0.01** | 0.23 | 1.00 | | Qwen3-14B $\rightarrow$ Qwen3-32B | **+0.23** | 0.26 | 1.44 | These complete 16-task comparisons quantify the behavioral change caused by expansion. We will add the pair-specific configurations, expansion-only results, noise construction, and calibrated claim to the revision.
AuthorsOpenReview ↗

Follow-up on validation selection, expansion, and perturbation controls

Thank you again for the concrete questions. We have now provided direct experimental answers to R2.1–R2.3:

ConcernNew evidence
Validation-based selectionOne validation-selected global checkpoint obtains 54.98 vs. 53.88 (+1.10) on held-out test data; task-wise validation selection obtains 55.97 (+2.09). The global gain has a paired task-level bootstrap 95% CI of [+0.07, +2.28].
Expansion aloneThe three expansion-only mean changes are -0.10, <0.01, and +0.23, showing that expansion approximately preserves aggregate performance and does not explain the main gain.
Matched noise controlsWith the same five-ratio search budget, ordinary Gaussian and support- and norm-matched Gaussian controls reach at most 54.42 and 54.65, respectively, versus 55.54 for donor injection (3B baseline: 54.59).
Pair-specific expansionWe reported the exact hidden-width, MLP-width, depth, attention-head, KV-head, and head-dimension mappings for all three model pairs, together with task-level output changes before and after expansion.

These experiments separate validation selection, dimensional expansion, generic perturbation, and structured donor injection. We have also calibrated “complementary capability transfer” as a hypothesis consistent with the evidence rather than a proven mechanism.

If these results resolve R2.1–R2.3, we would appreciate an updated assessment. Otherwise, we would be grateful for any specific point that still requires clarification.

Thank you for your response. The rebuttal partially addresses my concerns. I am maintaining my original rating of 2.

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