acceptodds
Under review as a conference paper at ICLR 2027

Learning Multi-Relational Graph Representations for DNA Methylation-Based Biological Age Estimation

Abstract

Aging clocks aim to estimate biological age, a measure of physiological state distinct from chronological age, from observable biomarkers, and are widely used for health assessment and disease analysis. DNA methylation is a particularly informative biomarker due to its stability and strong association with aging, and recent learning-based approaches have improved predictive performance. However, most existing methods treat CpG sites as independent features, overlooking the complex and heterogeneous biological relationships among them. We propose RelAge-GNN, a multi-relational graph neural network framework for DNA methylation-based age prediction. Our method constructs three complementary graphs capturing co-methylation patterns, genomic co-localization, and gene-level associations among CpG sites. Each graph is modeled by an independent GNN branch, and a learnable gating mechanism adaptively fuses the resulting representations. Experiments on large-scale datasets show that RelAge-GNN achieves competitive accuracy and stronger correlation with chronological age compared to state-of-the-art methods. Moreover, the model exhibits improved sensitivity in detecting age acceleration across diverse disease cohorts, highlighting its potential utility for disease characterization. Finally, through post hoc interpretability analyses, we quantify the contributions of different relational structures and CpG sites, providing biologically meaningful insights and suggesting potential directions for aging-related research. Our code is available at: https://anonymous.4open.science/r/RelAge-GNN-F1E3/.

Primary area:
applications to physical sciences (physics, chemistry, biology, etc.)
Keywords:
aging clock, graph learning

Reviews

Among:
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1234this paper, Bottom 10%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.67 over 3 reviews, above 10% of the others.
Reviewer_28LGOpenReview ↗
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1
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4
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2
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Paper summary

This paper propose RelAge-GNN, a multi-relational graph neural network framework for DNA methylation-based age prediction, which construct three complementary graphs to model relationships among CpG sites, capturing co-methylation patterns, genomic co-localization (i.e., whether two CpG sites are located on the same chromosome), and gene-level associations (i.e., whether two CpG sites are located within the same gene). In this paper, the model was trained on a dataset containing more than 3,000 samples; subsequently, several cohorts of varying sizes (each comprising hundreds of individuals) were selected to validate the model’s predictive error—the association between AA (age acceleration) positivity and three different diseases. However, the corresponding experiments did not support whether the new method he designed—namely, the additional subgraph structure—offered any obvious benefits.

Critical strengths

This paper proposes a multi-relationship graph neural network framework called RelAge-GNN for age prediction based on DNA methylation. This paper proposes an interesting research hypothesis: whether designing graph structures to capture gene-level associations and genomic associations of CpG sites can help improve the predictive capabilities of the aging clock and the prediction of health outcome endpoints.

Critical weaknesses

I could discuss this paper from two perspectives, but I believe there are some fundamental issues with both of them.

  1. From a biological perspective, the first problem is that the sample size is too small. Some contemporary studies have utilised larger sample sizes; many recent epigenetic clock studies have already included over 10,000 samples (NCAE-Age 2023 -13,647 samples , GPage-2023 &iTARGET -2024 -11,910 samples, AltumAge-2022-13,505 samples, DeepStrataAge 2026- 29,167 samples ... ...). Furthermore, the experimental scope is limited. This paper examined only three diseases. Compared with other relevant studies, it covers a very small number of diseases and health outcomes, and does not assess mortality. The findings for these three diseases lack sufficient support from statistical significance analyses. The assessment of disease is primarily based on whether age acceleration is greater than zero. AA>0AA>0 The study did not fully examine the relationship between continuous AA values and disease incidence through adjusted regression analysis. This means that the observed differences may reflect actual age differences between the different groups. For example, the higher proportion of positive AA results in the elderly group may have been mistakenly interpreted as a disease-related effect. The paper failed to adequately rule out this confounding factor. Therefore, I believe that the experiments can not support the proposed biomarker demonstrate any biomedical value. Furthermore, the authors did not examine whether additional intra-gene and intra-chromosomal graphs could enhance the health-related value of AA. If these graphs were intended to construct better biomarkers of ageing, the authors should have compared the impact of the resulting AA measurements on disease and health outcomes. The current experiments do not substantiate such added value.

  2. Algorithmic contribution and experimental design From an algorithmic perspective, the novelty is very limited. The experiments do not establish that the two additional designs intended to capture CpG interactions—whether sites belong to the same gene or lie on the same chromosome—provide useful additional information or a clear performance benefit. First, the model’s prediction error is worse than that of an existing model in the paper’s own comparison. Second, the ablation study does not establish that the complete model is the best configuration and the extra benefit of using all three graphs remains unclear. The baseline selection is also too narrow. Many relevant methods already have open-source implementations. Biolearn -2024 & ComputAgeBench -2025 contains numerous aging clocks (https://bio-learn.github.io/clocks.html , https://github.com/ComputationalAgingLab/ComputAge/tree/pre-release/computage/models_library/clocks ) that could be considered as baselines, but the paper does not compare against many of them. There are also several recent methods that are not adequately discussed or evaluated. Biolearn provides access to additional cohorts, while other studies already use much larger sample collections. The paper does not sufficiently justify its choices of datasets and baselines. The health-outcome experiments have the problems described above: they do not adequately establish a disease-specific effect, lack statistical support for the main improvements, and do not demonstrate useful additional information. The motivation for the method also appears to rest on an incomplete understanding of previous work. CpG measurements may enter a model as a vector, but the model can still learn interactions between CpG sites. Existing methods already do this. The authors also motivate their approach by referring to the risk of overfitting in deep learning. However, their own method is still a deep-learning model. Adding a more complex architecture does not automatically solve overfitting, improve interpretability, or turn the model into a white-box model.

Therefore, the experimental design does not support the claim put forward in this paper. Moreover, given the significant drawbacks in the experimental design, it falls far short of the publication requirements of ICLR.

Btw,the introduction discusses related work; however, it does not cite many of these works, citing only one piece of related work.

Questions for authors

Firstly, What criteria did the author use to select the baseline? Why were other compatible methods excluded Biolearn -2024 & ComputAgeBench -2025 ? (https://bio-learn.github.io/clocks.html , https://github.com/ComputationalAgingLab/ComputAge/tree/pre-release/computage/models_library/clocks )

Secondly, why did the author choose such a small sample size? Are these few cohorts sufficiently representative? What is the rationale for not comparing this study with other contemporaneous studies that have a larger total sample size?

Furthermore, in the author’s experimental design, why was only ‘age acceleration greater than 0’ assessed, rather than evaluating continuous predictive power—that is, the true ability to predict disease?

Do the age distributions differ across the various AA groups? Does the association with the disease persist after controlling for age, age-related prediction bias and cohort factors?

Given that existing methods are already capable of handling interactions between CPG points (even with vector inputs, the model architecture can handle this), What exactly does the three-graph structure add? Which comparisons and ablation studies demonstrate this incremental benefit?

3 comments

W1. Limited sample size, insufficient disease coverage, and insufficient biological validation

We agree that the current sample size and the evaluation of only three diseases are insufficient to establish broad biomedical utility. This study investigates whether explicit CpG relationships can support age prediction, but this architectural motivation does not by itself validate a biological aging biomarker. We will clarify the dataset inclusion criteria and representativeness, extend independent validation where compatible data are available, and explicitly acknowledge that mortality was not assessed. For disease analyses, we will move beyond AA positivity to continuous, healthy-reference-calibrated AA, using age-matched controls or covariate-adjusted models, and report effect sizes and confidence intervals. Given the small cohort size, the osteoporosis-related findings will remain exploratory. We will also compare the full model with G1-only and relationship-removal variants on the same adjusted disease analyses to determine whether the additional graphs contribute health-related information.

W2. Limited methodological novelty and insufficient experimental support

We acknowledge that the proposed contribution is an architectural integration of relationship-specific branches and adaptive fusion, rather than a new message-passing algorithm. The current results do not establish consistent superiority: AltumAge achieves lower MAE and MSE, and G1 alone also has lower MAE than the full model. However, our intended contribution is relationship-specific modeling. Biological age itself does not perfectly coincide with chronological age, so once the error is small enough, comparisons between models cannot be judged on this alone, because a perfect model should not be able to accurately predict chronological age in the first place; rather, it should accurately predict biological age. This is why we present age acceleration, which demonstrates the model's real utility, namely early disease detection. This is a practical task rather than an abstract error value, and it better demonstrates the model's capability, where we do indeed have an advantage. We will correct the corresponding statements and strengthen the evaluation by including compatible clocks from Biolearn and ComputAgeBench, as well as feature-matched non-graph models, merged-graph models, and uniform or fixed-weight fusion. We also agree that vector-based nonlinear models can learn CpG interactions; the intended distinction of this paper lies in the explicit use of relational priors, and their incremental benefit requires empirical validation.

Q1. Baseline selection criteria

The original baselines covered linear, deep feedforward, and graph-based aging clocks, but this coverage is not comprehensive. We will include additional compatible methods from Biolearn and ComputAgeBench, clearly specify requirements such as tissue, platform, CpG coverage, and prediction target, and clearly distinguish evaluation with published weights from retraining.

Q2. Sample size and cohort representativeness

The sample size reflects the public blood methylation cohorts assembled in this study; we have not established that it is sufficiently representative. We will clarify the inclusion criteria, report demographic and platform coverage, and seek additional independent cohorts. Comparisons with larger studies must account for differences in data composition and evaluation protocols.

Q3. Why evaluate AA positivity rather than continuous predictions?

AA positivity was intended as a descriptive metric, but it discards information and cannot establish disease predictive capability. We will evaluate continuous, calibrated AA through adjusted disease-state models, reporting effect sizes, confidence intervals, and discriminative ability. Cross-sectional data do not support claims about future disease incidence.

Q4. Age differences and persistence after adjustment

The current results cannot establish whether disease associations persist after controlling for age, prediction bias, and cohort effects. We will report age distributions for each group and conduct healthy-reference calibration and covariate-adjusted analyses. Any remaining disease associations will be stated only if these analyses support them.

Q5. Incremental benefit of the three-graph structure

We agree that vector-based nonlinear models can learn CpG interactions. The three graphs introduce explicit relational constraints and separated relationship-specific representations, but their incremental benefit remains insufficiently demonstrated. We will compare feature-matched non-graph models, merged-graph models, and fixed or uniform fusion, combined with repeated graph ablations, to isolate the value of this design.

Firstly, thank you for your thorough response; it appears you have carried out a great deal of supplementary experimentation, increasing the sample size and broadening the range of diseases covered in the paper, amongst other things. Of course, I am not certain whether this forms part of your future work or has already been completed.

If you have already completed this work, you may upload a new PDF, and I will consider awarding you additional marks at my discretion. To clarify, I would like to explain why I awarded you one mark. For this particular conference, I believe that to meet at least one of the ICLR acceptance criteria—which can be met in two respects—the paper should either demonstrate scientific value, that is, the observation of a new phenomenon, on a par with or exceeding that of top-tier journals in the field of ageing (excluding Nature Aging and Nature Communications I would not set the bar that high), or that you have made a significant methodological advance—in which case you would need to validate the performance of your method, whether in terms of speed, interpretability, or a substantial improvement in performance or accuracy, etc. As this is a top-tier conference in the field of computer science, I applied very high standards when reviewing your paper, However, at the same time, I would also like to point out that, as things stand, if you have completed the supplementary work you mentioned and discovered some interesting new phenomena that offer fresh insights to the community, I would be willing to raise your score. This is mainly because your core methodology will not change any further, so from the perspective of a methods paper, it does not meet the requirements of ICLR; however, if you wish to present it from the perspective of providing insights or scientific value, you must offer some interesting and broadly applicable insights within your extended results.

Thank you for clarifying your concerns and for your willingness to reconsider the paper based on additional evidence. We apologize that our previous response did not clearly distinguish planned revisions from completed work. We have not yet completed the additional experiments or obtained new results to report. In particular, expansion of the sample collection and disease coverage remains planned rather than completed. We are currently working on the supplementary evaluation and plan to proceed as follows:

Optimizing model performance. We plan to continue optimizing the model architecture to improve performance so that it can outperform all baselines as well as G1.

Continuous and adjusted AA analysis. We will evaluate healthy-reference-calibrated AA rather than relying primarily on AA>0. The analyses will examine age distributions and adjust for age, sex where applicable, and other available covariates, reporting effect sizes and confidence intervals. These will be interpreted as cross-sectional disease associations, not evidence of early detection or future disease incidence.

Health-related value of the additional graphs. Under the same evaluation protocol, we will compare G1-only, G1+G2, G1+G3, and the full model across repeated training seeds. We will assess both age-prediction errors and adjusted disease associations, directly testing whether adding the chromosome and gene relations provides information beyond G1.

We understand that completing additional experiments alone would not establish scientific value. The central question is whether relation-specific modeling reveals a consistent, independently reproducible pattern. We appreciate the opportunity to address your concerns.

Reviewer_w2HmOpenReview ↗
Rating
2
Confidence
3
Informativeness
3
Presentation
3
Soundness
3
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Paper summary

RelAge-GNN is a graph neural network that predicts DNA-methylation age using blood data from 37 GEO and ArrayExpress datasets, including 3,707 healthy and 624 disease samples. It models CpG sites using three graph structures based on co-methylation, chromosome location, and gene membership. Each graph is processed through a separate PNAConv branch, and a learnable node-level softmax gate combines their outputs. The model is compared with Horvath, AltumAge, DeepMAge, and GraphAge. Its clinical relevance is evaluated through age acceleration analysis in ovarian cancer, schizophrenia, and osteoporosis cohorts, while integrated gradients and branch masking are used to interpret model predictions and assess the contribution of each graph structure.

Critical strengths

Key strength of RelAge-GNN is its well-motivated multi-graph architecture, which separately models co-methylation, chromosome location, and gene membership through dedicated PNAConv branches and combines their representations using a learnable node-level softmax gate. RelAge design capture complementary biological relationships while accounting for degree heterogeneity in the graphs. RelAge benefits from a large and well-documented dataset comprising 37 GEO and ArrayExpress datasets, including 3,707 healthy and 624 disease samples.

Evaluation is strengthened by comparisons with established DNA-methylation age predictors, including Horvath, AltumAge, DeepMAge, and GraphAge, as well as comprehensive ablation experiments examining single-graph and pairwise graph removals and sensitivity to the co-methylation threshold. Besides, the application of age acceleration analysis to ovarian cancer, schizophrenia, and osteoporosis cohorts extends the investigation beyond age prediction, while integrated gradients and branch masking provide additional interpretability.

Critical weaknesses

Key concerns relate to the interpretation of Age Acceleration (AA), as the unadjusted difference between predicted and chronological age may be affected by regression to the mean, making claims of disease sensitivity unreliable without age residualization, healthy controls and uncertainty estimates.

Definition of sensitivity is also inadequate, the sign of AA is interpreted inconsistently, and disease results lack statistical testing, particularly for the small osteoporosis cohort. RelAge-GNN does not consistently outperform existing methods in age prediction, as AltumAge achieves lower MAE and MSE, while the reported advantage in correlation is insufficiently supported.

Ablation results also suggest that the co-methylation graph alone performs comparably to the full model, leaving the added value of multi-graph fusion unclear. Important comparisons, including a merged-graph baseline and fixed or uniform fusion weights, are missing.

Potential data leakage in graph construction and test-set selection of the co-methylation threshold further raise concerns about evaluation validity.

Branch importance may be confounded by differences in edge attributes and graph density, while the fixed-order node readout raises questions about permutation invariance and generalizability.

Missing training details and ambiguity about the validation strategy and baseline implementation. The inclusion of newborn and cord-blood samples may bias overall performance estimates, and BMIQ alone does not address cross-dataset batch effects. Besides age-stratified results appear inconsistent with the accompanying claims, and the interpretability analysis lacks adequate robustness checks to support strong biological conclusions.

Questions for authors

Report residualized AA and age-matched healthy controls for all disease analyses, with confidence intervals and specificity. What disease-to-healthy ratio is used in the mixed-cohort precision analysis? Missing training details and ambiguity about the validation strategy and baseline implementation. Is the co-methylation graph estimated using only training folds? Was the 0.7 threshold chosen on validation data? How does a single merged graph with all three edge types compare on the same backbone and parameter count? How do fixed or uniform fusion weights compare with the learned gate? What is the number of CpG sites N, and how would the readout change if N differed?

2 comments

Q1/Q2/W1. AA calibration, disease sensitivity, and mixed-cohort prevalence

We agree that raw AA is susceptible to age-related prediction bias and cannot independently establish disease sensitivity. We will use a healthy reference model and age-matched controls to evaluate residualized AA, report confidence intervals, specificity, and the actual disease/healthy proportions in each evaluated mixed sample. We will also harmonize the interpretation of positive and negative AA, and explicitly treat the small osteoporosis cohort as an exploratory result rather than evidence of clinical utility.

W2. Predictive accuracy and the claimed correlation advantage

We acknowledge that AltumAge achieves lower MAE and MSE, so the current results do not establish superior age prediction accuracy. Our intended contribution is relationship-specific modeling. Biological age itself does not perfectly coincide with chronological age, so once the error is small enough, comparisons between models cannot be judged on this alone, because a perfect model should not be able to accurately predict chronological age in the first place; rather, it should accurately predict biological age. This is why we present age acceleration, which demonstrates the model's real utility, namely early disease detection. This is a practical task rather than an abstract error value, and it better demonstrates the model's capability, where we do indeed have an advantage.

Q6/Q7/W3. How does the graph with three edge types differ from a single graph merging the three types

The current ablation experiments do not establish that the full model is superior in all respects: G1 alone achieves lower MAE, while the full model achieves lower MSE. We will revise the interpretation accordingly and compare against a merged graph under the same PNA backbone and a matched parameter budget, while adding uniform fusion and fixed-weight fusion as controls. These control experiments will disentangle the respective contributions of relationship separation, model capacity, and learned gating.

Q4/Q5/W4. Graph construction leakage and threshold selection

The notebook passes only the X_train of the selected fold into correlation estimation and reuses the resulting graph for validation and test. However, the current implementation cannot establish that 0.7 was selected using validation data only, and the reported threshold sweep cannot eliminate this concern. We will document the threshold selection history and adopt validation-only threshold selection in a rerun where the test set is never touched, rather than claiming that the current results already demonstrate a fully independent selection procedure.

W5. Confounders in branch importance comparisons

We agree that branch masking effects may reflect not only relational content but also differences in graph density and edge attributes. We will therefore describe these effects as measures of model dependence rather than direct biological importance. Density-controlled comparisons, edge-attribute controls, and repeated masking analyses will help assess whether the observed ordering still holds after accounting for these factors.

Q8/W5. Fixed-order readout, permutation invariance, and changing the CpG panel

The implementation uses N = 20,318 CpGs in a fixed and aligned order. Although message passing is permutation-equivariant, the flattened readout is position-dependent and requires consistent CpG ordering across samples. Changing N would require replacing and retraining the first readout layer; the current checkpoint cannot directly support an arbitrary panel. We will clearly state this limitation and distinguish the current design from permutation-invariant pooling readouts.

Q3/W6. Training details, validation strategy, and baseline implementation

We agree that the experimental description is insufficiently precise. The notebook creates a test holdout for each dataset and then selects a single training/validation fold, which should not be described as a completed five-fold evaluation. We will document the exact splitting scheme, checkpoint selection criteria, training settings, and whether each baseline was retrained or used published weights. The revised evaluation will select checkpoints based on validation performance only and evaluate the test set after model selection is complete.

Thank you for the detailed response. Co-methylation graph was estimated using only the training samples in the selected fold addresses my concern about leakage during graph construction. The authors also explain the fixed ordering of the 20,318 CpGs and clarify that the reported results come from a single training/validation fold. Three concerns remain central to my assessment ; such as Age acceleration and early disease detection. I agree that chronological-age prediction error alone cannot establish how well a model captures biological age. The same reasoning applies to prediction error in a disease cohort. The response proposes residualized AA, age-matched healthy controls, confidence intervals, and specificity, but provides no results from these analyses or the disease-to-healthy ratio used to calculate precision. Even if calibrated AA distinguishes patients from controls, a claim of early detection requires evidence that the signal precedes diagnosis. I therefore find the claim of an advantage in early detection premature. Added value of multi-graph fusion. The co-methylation graph alone achieves lower MAE, while the full model achieves lower MSE. This leaves open whether separating the three relationships and learning their fusion weights improves performance. The proposed parameter-matched merged-graph baseline and fixed or uniform fusion controls directly address this question; and threshold selection and evaluation. The response leaves unresolved whether test performance influenced the choice of the 0.7 threshold. I would welcome results from the proposed validation-only selection procedure, with the threshold and checkpoint fixed before test evaluation, together with clarification of how each baseline was evaluated.

Reviewer_9PFHOpenReview ↗
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2
Confidence
3
Informativeness
1
Presentation
2
Soundness
2
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Paper summary

This paper proposes RelAge-GNN for DNA-methylation-based age prediction. The method represents CpG sites using three relation-specific graphs: co-methylation, same-chromosome, and same-gene relations. Separate PNAConv branches encode the three graphs, and a node-wise gating network fuses their representations before age regression. The paper also presents post-hoc feature/node/graph importance analyses and evaluates age acceleration (AA) in several disease cohorts.

The topic is relevant and the attempt to distinguish different biological relations is reasonable. However, I have substantial concerns about the experimental protocol, the strength of the empirical claims, and the level of methodological novelty. In its current form, I do not find the evidence sufficient to support the main conclusions.

Critical strengths
  • The paper addresses a meaningful application of graph learning: DNA methylation-based aging clocks.
  • Separating co-methylation, genomic-location, and gene-level relations is more interpretable than merging all edges into a single homogeneous graph.
  • The authors include ablations over the three graphs and discuss limitations and ethical considerations.
  • The manuscript is generally easy to follow at a high level.
Critical weaknesses
  1. The data splitting protocol may substantially overestimate generalization.
    Healthy samples from 37 GEO/ArrayExpress datasets are randomly divided into train/validation/test splits. This means samples from the same cohort, study, platform, laboratory, and potentially preprocessing batch can occur in both training and test sets. For methylation data, this is a serious concern because cohort and platform effects can be strong. A random sample-level split does not demonstrate cross-cohort or cross-platform generalization. At minimum, the paper should report leave-one-dataset-out or group-based splits by dataset/platform, with all preprocessing and graph construction performed within each training fold.

  2. Potential leakage in construction of the co-methylation graph is not resolved.
    The paper states that a large healthy sample set is used to estimate inter-site correlations, but it is unclear whether the co-methylation graph is computed using only training samples for each fold. If test samples contribute to correlation estimation, the test distribution is used during training, even if labels are not used. This is particularly problematic because the graph is a central component of the proposed method. The manuscript needs an explicit fold-wise graph-construction protocol and a comparison between train-only and full-data graph construction.

  3. The claimed predictive improvement is not supported by the reported primary error metrics.
    In Table 2, RelAge-GNN has better FRC than the baselines, but its MAE (3.43) and MSE (29.46) are both worse than AltumAge (MAE 3.30, MSE 28.31). Thus, the method does not outperform the strongest reported baseline on the standard regression metrics. The paper should not describe this as enhanced precision or superior predictive accuracy without statistical evidence. Moreover, no confidence intervals, standard deviations, results over random seeds, or statistical tests are reported.

  4. The disease/age-acceleration conclusions are not sufficiently controlled.
    The disease experiments use raw AA=y^−yAA = \hat y-y, and evaluate quantities such as the fraction of samples with AA>0AA>0. This is difficult to interpret without correcting for age-dependent prediction bias, cohort effects, sex, platform, cell-type composition, and other confounders. AA is typically calibrated relative to suitable healthy controls or derived from residualized models. A higher fraction of positive raw residuals does not by itself establish improved sensitivity to disease-related aging. The “precision” analysis is also unclear: the disease prevalence in the mixed evaluation set, the sampling procedure, and confidence intervals are not reported. The stated clinical/disease-characterization conclusions should be substantially toned down unless supported by matched controls, statistical testing, and covariate-adjusted analyses.

  5. Novelty over GraphAge appears limited.
    According to the paper’s own description, GraphAge already uses co-methylation, same-chromosome, and same-gene relations. The main difference seems to be processing each relation in an independent PNA branch followed by gated fusion. This is a reasonable architectural variant, but it is incremental relative to established multi-relation/multi-view GNN designs. The paper should more carefully isolate the value of independent branches, PNAConv, and the gating module. Comparisons to standard relational-GNN baselines, relation-aware attention/fusion, and simple late-fusion baselines are needed.

  6. Several technical details are unclear or inconsistent.
    Equation (6) defines Wm∈RN×1W_m \in \mathbb{R}^{N\times1} while applying it to Hf∈RN×64H_f\in\mathbb{R}^{N\times64}, which is dimensionally inconsistent; presumably the weight should map 64 channels to one scalar per node. The paper should clarify the exact number of CpGs/nodes, edge counts and densities for every graph, whether same-chromosome edges form complete chromosome-wise cliques, the correlation threshold selection procedure, and the scalability of PNAConv on these graphs. The claim that the same-chromosome and same-gene graphs are sparse also needs quantitative support.

  7. The interpretation results are descriptive rather than validated.
    Integrated gradients and branch occlusion can be useful exploratory tools, but they do not establish biological importance or causal relevance. The current conclusions about structural drivers and aging mechanisms are too strong. At minimum, the authors should test explanation stability across folds/seeds and provide enrichment or external validation for the highlighted CpGs.

Questions for authors
  • Was the co-methylation graph recomputed using training samples only in every fold?
  • Are samples from the same GEO accession ever split across train and test?
  • Why is the full model described as best in Table 3 when w/o G2 has lower MAE (3.39 versus 3.43)?
  • How is FRC defined exactly, and why do some ablated models have FRC values above 1?
  • What is the disease prevalence in the mixed disease/healthy “precision” experiment, and what are the confidence intervals for all AA-based results?
  • Can the method retain its benefit under leave-dataset-out and leave-platform-out evaluation?
2 comments

Q2/Q6/W1. Sample-level splitting and cross-cohort generalization We acknowledge this limitation. Under our protocol, samples sharing the same GEO accession may appear in both train and test sets. Thus, our results evaluate within-cohort prediction, not cross-cohort generalization. We will state this scope clearly and add dataset/platform-held-out evaluations, fitting all preprocessing and graphs only on training partitions.

Q1/W2. Potential leakage in co-methylation graph construction The graph is built from X_train within the selected fold and reused for validation/test; validation/test samples are not passed into correlation estimation. However, we only evaluated a single fold. We will clarify this, document graph/checkpoint provenance, and add a leakage diagnostic comparing training-only vs. full-data graph construction.

W3. Predictive superiority and missing uncertainty estimates We agree Table 2 does not establish superior accuracy (AltumAge has lower MAE/MSE). Our contribution is relationship-specific modeling. Since biological age does not perfectly coincide with chronological age, a perfect model should not accurately predict chronological age, but rather biological age. Thus, we focus on age acceleration for early disease detection—a practical task where our model shows advantages. We will replace claims of superior accuracy with practical utility, and report results over multiple random seeds with 95% CIs for paired differences.

Q5/W4. Uncontrolled AA analysis and unclear disease prevalence We agree raw AA positivity alone cannot establish clinical sensitivity. We will report actual case/control numbers, sampling procedures, and CIs. Where metadata allow, we will use healthy-reference calibration and covariate-adjusted analyses for continuous AA, treating disease findings as exploratory until supported.

W5. Limited novelty relative to GraphAge and insufficient architectural controls Our contribution is explicitly separating biological relationships into independently parameterized branches with node-level adaptive fusion, rather than new operators. We will state this narrower scope and add controlled comparisons with merged graphs, standard relational GNNs, and alternative fusions to isolate measurable gains.

W6. Dimensional inconsistency and incomplete graph specification Thank you for catching this. Under under the notation Hf×WmH_f \times W_m, the shape of WmW_m should be 64×164 \times 1, not N×1N \times 1. The current code uses 20,318 CpG nodes, and its chromosome graph additionally requires ∣r∣>0.7|r| > 0.7;, thus it is not a complete clique. We will align the text with the code, report exact edge counts/densities, document threshold selection, and provide runtime/memory metrics.

W7. Interpretation does not establish biological or causal importance We agree attribution and masking reflect model dependence, not causal mechanisms. We will revise these claims, assess explanation stability across seeds and held-out cohorts, and evaluate CpG enrichment against the background panel (accounting for probe mapping and multiple testing). Biological conclusions will remain exploratory.

Q3. The full model is not the best configuration on all metrics Removing G2 improves MAE (3.43 →→ 3.39), and G1 alone is even lower (3.35). The full model only has the lowest MSE. We will correct the self-contradictory statement in Sec 5.6, framing it as a trade-off, and verify the incremental value of extra relationships via repeated runs.

Q4. Definition of FRC and values greater than 1 FRC is the slope aa in \hat{y} = a * y + b, not Pearson correlation. It is not bounded by 1; >1>1 indicates predicted age scale expansion. We will rename it "calibration slope," provide the explicit definition, report intercept/CIs, and correct the claim that "the full model is always closest to 1" (since w/o G2 has a slope of 1.007).

The authors provided a highly constructive and honest rebuttal that directly addresses my core concerns regarding data splitting, potential leakage, and overclaimed predictive superiority and causality. I appreciate their commitment to reframing the contribution around practical utility and age acceleration, correcting technical inconsistencies, and treating biological interpretations as exploratory. While the single-fold evaluation and architectural novelty relative to existing methods remain limitations, the proposed revisions—specifically the addition of held-out evaluations, leakage diagnostics, and controlled architectural comparisons—are concrete and scientifically sound. Therefore, I will maintain my current score.

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