Lifestyle change accelerates epigenetic ageing in King penguins

Domain: biology
Published: 2026-03-11
Editorial outcome: minor_revision

Abstract

Introduction

Results

Methods
≥ 0.2 and a p-value ≤ 0.05 (10,205 CpGs).

compared to wild individuals) and possible intercepts (relative age acceleration) ranging from -15 to 15 years. We also tested elastic net α mixing parameter values ranging from 0 to 1, with parameter range and step size decremented iteratively.

Peer review rounds
[{"round": 1, "reviewer_comments": {"reviewer_2": "I thank the authors for the clarifications provided. While my main expertise does not lie in mathematical modeling, the explanations given in response to the issues raised by other reviewers appear sound. Similarly, while it is unfortunate that other (metabolic) health metrics – some of which could also be assessed from blood samples – as well as transcriptional data are entirely missing, I understand that obtaining such data can be both technically and logistically challenging. Some remaining comments from my side:\n1. I want to stress again a point that might not have come across as clearly as I wanted previously. Looking at the broad picture, CR is one of the primary reasons for choosing this species as a novel model organism, as it is nicely described in the text. However, because the transition to zoos necessarily comes with so many other lifestyle changes, this leaves us in a situation where nothing can actually be concluded with respect to CR per se. Now, this does by no means delegitimize the work shown – I do think, there is value in introducing this model. As far as I can tell, there are no false claims made regarding this, either. But reading through the introduction, which specifically points out the debate around CR effects in long-lived species, sets some expectations, which – to me – are not met. This is an issue of framing and could be resolved by (for example) addressing this limitation directly in the Discussion.\nOther than that, I support the effort and the prospect of testing this by reintroducing fasting periods at the zoo.\n2. The distribution of sampling dates in the wild (now Supplementary Figure 1.) does indeed show a broad distribution, but I would still argue that the main part of the samples was collected somewhat closely to the end of the fasting period. While the epigenome is of course very dynamic, DNA methylation is still relatively stable. In that sense, it would be interesting to see how different the methylation patterns would look, were the samples collected at a time point shortly before the fasting period similar to Zoo Zurich. I assume the younger birds that do not engage in breeding in the wild will also not undergo the associated fasting.\n3. I assume that for the zoo-housed animals, there must be some health data available based on veterinary care. Is there no way (with existing data) to validate the relevance of EAA for physical wellbeing in this new model. Could that be shown or commented on.", "reviewer_3": "The authors have responded in detail to the comments of the reviewers. I remain interested in the dataset and the findings.\nOn the one hand, despite the extensive responses, I strongly believe that the author’s preferred approach to a clock is incorrect. It is highly prone to overfitting and it is not truly replicated here (no animals in the wild). When using a biased approach to model building (assume differences exist), much of the statistical arguments used in response to reviewer one are poor substitutes to the standard in the field - replication in a different dataset. As an aside, the discussion about linear vs. logarithmic makes a wrong assumption – that all CpG sites behave the same with aging. They just don’t – the “logarithmic” model applies best to loci that change during development. Many loci (e.g. promoter CpG islands) don’t change much with development and instead show very clearly linear methylation change with age.\nOn the other hand, I applaud the author’s unbiased approach based on average CpG methylation (page 8 of the response). In my opinion, the fact that age acceleration in this analysis is much lower than previously found (2.6 years vs. 6.5 years) is not due to lower sensitivity but to lower proneness to overfitting. I would still like to hear more about this approach and its results – for example, why the focus on “negative correlation with age”? Some datasets suggest that loci that gain methylation with age have a different biology (and perhaps higher accuracy for aging) than loci that lose methylation with age (more prone to cell type effects). I also don’t fully understand the rescaling approach – if loci are selected based on R values, why does the average value matter and why does it need to be rescaled? One can directly fit a linear model to estimate a methylation age and then calculate age error in each individual – predicted to be positive in the wild and negative in the zoos. As a bonus, this approach allows the authors to much better define the most relevant set of aging loci to dissect the differences between zoo and wild animals (CpG islands? Promoters? Repetitive elements?). I would strongly suggest that Fig. 1 of the paper should be based on this unbiased approach rather than the biased (and possibly overestimating) method first used.\nThe aDMS PCA (page 17 of the response) is interesting but should be labelled by age (or decade). Have the 4 outliers in this PCA (top right) been excluded from subsequent analyses? I would also suggest showing a PCA of all loci with decent coverage before showing the aDMS PCA. Does an “unselected” PCA show effects of aging/zoo etc.?\nResponses to other issues raised are appropriate.", "reviewer_4": "The authors have clearly and satisfactorily addressed all of the comments I raised in the previous round of review.", "reviewer_5": "To the Authors,\nThank you for your diligent work and for the detailed responses to the reviewer's comments. I have carefully considered your explanations, particularly regarding the interpretation of epigenetic age acceleration (EAA) and your methodological validations. While I appreciate the effort, I remain unconvinced by certain aspects, and I believe further clarification and additional data are essential to fully support your conclusions.\nMy primary reservations revolve around three key areas:\n1. Interpretation of Intercept-Only Differences in Epigenetic Age: You propose that the observed intercept difference, rather than a slope difference, aligns with a logarithmic model where a constant acceleration factor manifests as an intercept shift. However, my concern persists regarding its biological interpretation within the same species under different conditions. If a true and sustained difference in the rate of biological aging exists due to lifestyle, it should fundamentally lead to a divergence in aging trajectories, reflected as a slope difference over time. The parallel lines, even if mathematically consistent with a logarithmic model, suggest a baseline offset established early, raising strong suspicions of subtle, uncaptured batch effects related to sample origin or handling, despite your rigorous efforts in sample distribution and covariate adjustment.\n2. Lack of Early-Life Data and Implications for Non-Linear Analysis: Your acknowledgment that the logarithmic approximation \"is not correct for very early life\" and that \"these early ages are not sampled at all at the zoo\" is a critical point. If the intercept difference is indeed a result of rapid initial acceleration in early development, then the most crucial data for observing and accurately modeling this phenomenon is missing. Without epigenetic data from very young animals in both environments, any non-linear analysis of aging trajectories remains speculative. This limits definitive conclusions about the precise timing and impact of early-life lifestyle factors on epigenetic aging.\n3. Clarity of Training and Test Sets: I find the explanation regarding the training and testing of your epigenetic clock model to be insufficient. While leave-one-out cross-validation (LOOCV) is a valuable internal validation technique for assessing model performance within a given dataset, it does not substitute for a truly independent, external test set. Without demonstrating the model's predictive power on a completely unseen and separate dataset (e.g., new samples collected independently), the analysis, particularly the significance of the age acceleration plots, remains less convincing.\nFurthermore, a shared training set might obscure a true difference across these groups; a more revealing approach might involve training a clock exclusively on either the zoo or wild samples and then applying it to the other group. It is imperative to clearly delineate the training and test sets used, and if a fully independent external test set was not employed for the penguin data, this should be explicitly stated as a limitation.\nIn conclusion, while I commend the innovative approach of using King penguins as a model, these points need critical attention. I strongly recommend providing explicit clarification and transparency regarding the training and test sets used for the penguin epigenetic clock, and generating and incorporating epigenetic data from very young animals (birth to early developmental stages) from both wild and zoo populations. This is crucial for a robust non-linear analysis and to definitively support your interpretation of age acceleration. Until these fundamental data gaps and methodological clarifications are addressed, definitive comments on the causal relationship between lifestyle and epigenetic age acceleration remain premature and potentially an overstatement.\nSincerely,"}, "author_response": ""}, {"round": 2, "reviewer_comments": {"reviewer_2": "We thank the authors for their clarifications. With respect to the distribution of sampling dates, if I understand correctly, the bimodal distribution of sampling of the zoo group could potentially still obscure subtle effects. That being said, this effect (should it exist) would likely be minimal. The proposed addition to the Discussion seems therefore appropriate. With that, all my comments have been addressed.", "reviewer_3": "I have no further suggestions.", "reviewer_7": "Cristofari compared epigenetic aging trajectories between king penguins housed in zoos to those from wild animals. This is a unique project with a rarely studied animal species that has the potential to reveal new insights into how lifestyle factors accelerate, or slow down aging processes and the DNA methylation based epigenetic clocks of aging. One important aspect of this work that I didn’t see much emphasized is that the authors employed whole genome methylation sequencing (EM-seq) rather than the much more commonly used Illumina arrays which have limited genome coverage. I found the data in this manuscript interesting and convincing. The authors provided satisfactory responses to the reviewers’ comments including those made by reviewer #5."}, "author_response": "NCOMMS-25-30818A\nReviewer #2 (Remarks to the Author):\nI thank the authors for the clarifications provided. While my main expertise does not lie in mathematical\nmodeling, the explanations given in response to the issues raised by other reviewers appear sound.\nSimilarly, while it is unfortunate that other (metabolic) health metrics – some of which could also be\nassessed from blood samples – as well as transcriptional data are entirely missing, I understand that\nobtaining such data can be both technically and logistically challenging. Some remaining comments from\nmy side:\n1. I want to stress again a point that might not have come across as clearly as I wanted previously.\nLooking at the broad picture, CR is one of the primary reasons for choosing this species as a novel model\norganism, as it is nicely described in the text. However, because the transition to zoos necessarily comes\nwith so many other lifestyle changes, this leaves us in a situation where nothing can actually be\nconcluded with respect to CR per se. Now, this does by no means delegitimize the work shown – I do\nthink, there is value in introducing this model. As far as I can tell, there are no false claims made regarding\nthis, either. But reading through the introduction, which specifically points out the debate around CR\neffects in long-lived species, sets some expectations, which – to me – are not met. This is an issue of\nframing and could be resolved by (for example) addressing this limitation directly in the Discussion.Other\nthan that, I support the effort and the prospect of testing this by reintroducing fasting periods at the zoo.\nWe agree with this important nuance, and have added the following to our discussion (lines 302-307):\n“Naturally, the changes associated with the transition to zoo conditions are broad and multifaceted,\nextending beyond reduced caloric intake and physical activity. While this study demonstrates the impact of\nthis transition on ageing rate, and suggests that metabolic regulation is deeply involved, the precise\nmechanisms through which this impact happens remain to be explored - whether through CR, sedentary\nbehaviour, disruption of life rhythms, reduced environment complexity, altered microbial environment, or\nother factors.”\n2. The distribution of sampling dates in the wild (now Supplementary Figure 1.) does indeed show a\nbroad distribution, but I would still argue that the main part of the samples was collected somewhat\nclosely to the end of the fasting period. While the epigenome is of course very dynamic, DNA methylation\nis still relatively stable. In that sense, it would be interesting to see how different the methylation patterns\nwould look, were the samples collected at a time point shortly before the fasting period similar to Zoo\nZurich. I assume the younger birds that do not engage in breeding in the wild will also not undergo the\nassociated fasting.\nThank you for raising this interesting point. We are currently engaged in answering this question through\nexperimental fasting in zoo settings. Unfortunately, our wild sampling efforts are currently suspended\ndue to the highly pathogenic avian influenza epizootic, but we hope to resume them as soon conditions\npermit.\nIn the meantime, the circannual cycle is indeed known to be reflected in birdsʼ methylome, as shown for\nexample by Lindner et al. (2020). While our dataset was not explicitly designed to capture this, we do\nobserve seasonal variation. Specifically, we use elastic net regression to relate the day of the season\n(defined as October 1st for the Southern Hemisphere and April 1st for the Northern Hemisphere) to the\nprincipal components derived from the whole-methylome PCA. The day of the season can be accurately\npredicted based on the methylation variation (with a pseudo-R-squared of 0.89, see panel A). However,\nthe total amount of CpG methylation variance explained is only 4.97% (calculated as the product of the\nsquared elastic net regression weights by PCA eigenvalues, summed over all PCs, and divided by the sum\nof eigenvalues). Moreover wild and zoo birds do not significantly differ along this seasonal axis (panel B),\nand “origin”does not significantly contribute to the fitted linear model.\n1 of 11\nNCOMMS-25-30818A\nIn summary, we find that (1) indeed, the point in the breeding cycle at which a bird is sampled leaves a\nsignature in that birdʼs methylome (as expected), (2) that seasonal signal reflects only a minor part of the\ntotal variance in CpG methylation, and (3) there is no evidence for a systematic bias in our samples due to\nsampling dates between wild and zoo groups. However, we added the following to our discussion (lines\n316-320): “the sampling dates are not entirely standardised in our study relative to the onset of the\nbreeding season. All samples have been collected during the breeding season, and dates do not\nsignificantly differ between groups: but the epigenome is known to change with the circannual cycle\n(Lindner et al. 2020), and this incomplete standardisation may introduce some noise - although likely not a\nsystematic bias - into our results.”\n3. I assume that for the zoo-housed animals, there must be some health data available based on\nveterinary care. Is there no way (with existing data) to validate the relevance of EAA for physical wellbeing\nin this new model. Could that be shown or commented on.\nThis would indeed have been ideal. Unfortunately, such data currently do not exist. Although there is an\nongoing effort to log veterinary interventions more systematically in electronic databases, this is far from\ncovering the past 40 (or even 15) years, and veterinary logs do not follow individuals if or when they are\ntransferred between zoos. This lack of systematic recording leads to biases in the data which tend to\nfocus more on certain types or levels of pathology. Consequently, our understanding of the health history\nof the zoo-housed penguins in this study is limited to anecdotal information. This project has actually\nfacilitated discussions about this shortcoming, and we hope that future initiatives will enable more\nsystematic and comprehensive health data collection .\nReviewer #3 (Remarks to the Author):\nThe authors have responded in detail to the comments of the reviewers. I remain interested in the dataset\nand the findings.\nOn the one hand, despite the extensive responses, I strongly believe that the authorʼs preferred approach\nto a clock is incorrect. It is highly prone to overfitting and it is not truly replicated here (no animals in the\nwild). When using a biased approach to model building (assume differences exist), much of the statistical\narguments used in response to reviewer one are poor substitutes to the standard in the field - replication\nin a different dataset.\nWe agree that replication in a different dataset would be the “gold standard” to demonstrate the\nrobustness of our results. However, as in many studies, particularly those relying on genomic data, there\nare limitations on the available sample size: allocating samples to a test set reduces the power on\ntraining. This constraint guided our choice of using a leave-one-out approach for training/test design (i.e.,\n63 training samples and one test sample for each point). We acknowledge that this approach cannot fully\n2 of 11\nNCOMMS-25-30818A\nsubstitute for validation in a completely independent wild population. As we have emphasized in our\nprevious response, however, a different known-age dataset in the wild simply does not exist. We made\nevery effort to minimize batch effects, as discussed in earlier responses, but ultimately, we agree that, as\nin many cases, only a fully independent replication of this study will settle this point entirely.\nThanks to a suggestion made by Reviewer 5, we also provide an additional form of independent\nvalidation of our approach. Specifically, we trained the epigenetic clock model solely on all zoo samples,\nand then used it to predict the ages in all wild samples, or vice versa. These two approaches yield very\nsimilar results, and are highly consistent with our main analyses (see below for details, and\nSupplementary Figure 7 along with the accompanying text). While this is not a substitute for a full\nreplication study, we believe it will address the concerns about potential overfitting. This method, similar\nto the mean-aDMS approach, should be entirely immune to group overfitting.\nWe now explicitly acknowledge this limitation in the discussion (lines 311-323): “This study has three\nadditional methodological limitations: [...] Third, we include two zoos, but only one wild population - as\nthere is currently only one known-age wild King penguin population covering the whole age span of King\npenguins in the world (Bardon et al. 2023). This study thus lacks a fully independent biological replicate in\nthe wild.”\nAs an aside, the discussion about linear vs. logarithmic makes a wrong assumption – that all CpG sites\nbehave the same with aging. They just donʼt – the “logarithmic” model applies best to loci that change\nduring development. Many loci (e.g. promoter CpG islands) donʼt change much with development and\ninstead show very clearly linear methylation change with age.\nThis may be a misunderstanding: we do not make the assumption that all CpG sites behave the same with\naging. We fully agree with the reviewer that some loci have a marker logarithmic trajectory, some behave\nlocally linearly in adulthood, and some follow apparently stochastic trajectories. In theory, however, it is\nimpossible for methylation at any single CpG to be truly linear with age: methylation levels are bounded\nbetween 0 and 1, but a strictly linear change would imply the existence of methylation values outside of\n[0,1]. We point to a recent article by Ochana and colleagues (Cell Reports 2025,\n10.1016/j.celrep.2025.115958), which provides convincing examples at the CpG level.\nHere we rather make the point that epigenetic age, which is a methylome-wide index, follows a\nlogarithmic relationship with time. This general behaviour of epigenetic clocks has been well\ndocumented, as we briefly mentioned in our previous answer. We agree that this logarithmic pattern is\nmost prominently observed during development (it was initially thought to be primarily relevant before\nage 20 in humans, see Horvath et al. 2013). This is largely because the logarithmic curve becomes harder\nto distinguish from a straight line, when we focus on a small range of larger predictor values (typically, a\nrange of adult ages).\nThis actually justifies our choice of model, when we approximate epigenetic age by a straight line in our\nanalysis, in full agreement with the reviewerʼs perspective. Our point about the logarithmic model is less\nrelevant for interpreting the shape of the EA curve, that interpreting the intercept shift, that we discussed\nin our previous revision.\nOn the other hand, I applaud the authorʼs unbiased approach based on average CpG methylation (page 8\nof the response). In my opinion, the fact that age acceleration in this analysis is much lower than\npreviously found (2.6 years vs. 6.5 years) is not due to lower sensitivity but to lower proneness to\noverfitting.\nWe thank the reviewer once again for suggesting that we include this simpler approach in the first place!\nIndeed, we agree it provides stronger support for the main result. Regarding the magnitude of the\nobserved effect, we do agree this remains an open point for discussion. On one hand, the smaller, more\n3 of 11\nNCOMMS-25-30818A\nconservative estimate is a reliable “lower bound” for the effect of zoo lifestyle, which we now underline in\nour manuscript.\nOn the other hand, in our human test data, our approach produces estimates that closely align with the\nwell-established PCPhenoAge and PCGrimAge clocks (see Supplementary Figure 8 C-D and accompanying\ntext: “Final mean difference between groups was 11.8 years according to our model (SE = 1.24, p-value <\n1e-12), to be compared with 14.0 years according to PCPhenoAge (SE = 0.64, p-value < 1e-16) and 11.6 years\naccording to PCGrimAge (SE = 0.57, p-value < 1e-16).”) This does not suggest our model does not overfit /\noverestimate inter-group differences. Furthermore, the mean-aDMS approach aggregates sites with equal\nweights, including strong and weak predictors of age.: We expect it to have a somewhat lower predictive\npower compared to models that incorporate a larger part of covariance with age. For these two reasons,\nwe think the 6.5 years estimate is likely to be accurate in this case.\nIn both cases, the estimates lead to a qualitatively identical conclusion, and we suggest to provide both,\ntogether with interpretative context, in our manuscript at lines 143-149:\n“The numerical differences between these approaches may be explained by different sensitivities (training\nsample size is halved in the first of these controls, and the second one is based a cruder averaging\nprocedure that gives equal weights to all included aDMS CpGs, regardless of the strength of their actual\ncovariance with age).. The true value of the age acceleration at the zoo is thus likely between 2.63 years (the\nmost conservative estimate) and 6.48 (the estimate derived from a PCA of the whole sample set) - in any\ncase, we reach the conclusion that zoo-housed birds are significantly age-accelerated compared to their\nwild counterparts.”\nWe also amended the numbers in our discussion accordingly at lines 330-331.\nI would still like to hear more about this approach and its results – for example, why the focus on\n“negative correlation with age”? Some datasets suggest that loci that gain methylation with age have a\ndifferent biology (and perhaps higher accuracy for aging) than loci that lose methylation with age (more\nprone to cell type effects).\nWe appreciate the reviewer's insightful comment regarding the focus on loci with a negative correlation\nwith age. We fully agree with the reviewer that CpGs with positive and negative correlations with age\nshould not be considered as biologically homogeneous. Indeed, Horvath (2013, Genome Biology) already\nproposed that loci with positive correlation to age tend to exhibit less variance across tissues, although\nthis effect was most pronounced in fetal tissues rather than in adults) More recent studies (Moqri et al.\n2024, Nat. Com.) have convincingly demonstrated that polycomb repressive complex 2 (PRC2) targets\nconsistently gain methylation with age and serve as reliable epigenetic aging biomarkers .\nIn our original PC-elastic-net analysis, we included both positively and negatively-correlated CpGs.\nHowever for the “validation” analysis we opted to focus solely on negative correlation loci. This choice\nwas driven by the distribution of CpGs in the King penguin genome, where only 366 CpGs exhibit a strong\npositive Pearson correlation with age, compared to 9,839 with negative correlation. This is notably\ndifferent compared with Horvath's original clock, where > 50% of clock-sites show positive correlations\nwith age. These CpGs are not all independent either, for example, 94 CpGs with positive correlation with\nage are grouped in just 4 loci. And while it would have been extremely interesting to replicate e.g. the\nPRC2-AgeIndex approach described by Moqri et al (2024, Nat. Com.), we lack direct PRC2 binding\ninformation in this non-model species. Hence, in our case, conclusions derived from these comparatively\nfew positive-correlation sites would unfortunately not be robust.\nThis being said, this difference from human data merits further exploration and could provide valuable\ninsights into species-specific epigenetic ageing mechanisms.\nI also donʼt fully understand the rescaling approach – if loci are selected based on R values, why does the\naverage value matter and why does it need to be rescaled? One can directly fit a linear model to estimate\n4 of 11\nNCOMMS-25-30818A\na methylation age and then calculate age error in each individual – predicted to be positive in the wild\nand negative in the zoos.\nWe apologize for any lack of clarity in our previous explanation - this is actually what we did in the\nprevious revision. To clarify, the rescaling was not applied at the individual CpG level, but was performed\non the average methylation of the selected aDMS, prior to the linear modelling. This rescaling is\nperformed to provide model coefficients that are directly interpretable, with age acceleration expressed\nin units compared to chronological age. We agree that in this case, this rescaling could also have been\nperformed on the coefficients after the linear regression without loss of information.\nWe have edited the main text to make this clearer (lines 136-137):\n“The average methylation value across aDMS sites was linearly scaled to the observed range of ages in our\ndata, and linearly modelled as a function of log(age)”\nAs a bonus, this approach allows the authors to much better define the most relevant set of aging loci to\ndissect the differences between zoo and wild animals (CpG islands? Promoters? Repetitive elements?). I\nwould strongly suggest that Fig. 1 of the paper should be based on this unbiased approach rather than\nthe biased (and possibly overestimating) method first used.\nWe are not sure we entirely understand the suggestion. On the one hand, using the full methylation\nmatrix as a predictor in a single model would lead to a problem of degrees of freedom. It is precisely to\navoid this that we used feature preselection in our original analysis (based on Pearson coefficient and\nelastic net regression, which is a standard choice in the field). On the other hand, fitting one model per\nCpG site (an Epigenome-Wide Association Study (EWAS)-like approach) is possible: that is what we did for\nfeature pre-selection. But it is unclear how the individual-level residuals (not per-CpG, per-individual\nlevel) are obtained in that case. While we agree developing the EWAS aspect further is an extremely\ninteresting approach, we believe it would not directly add to this study, which focuses on the difference in\nageing rate between lifestyle groups, not on the impact of ageing itself on the epigenome.\nIn this revised version, we have included the approach suggested above by the reviewer (a linear model of\naverage aDMS methylation as a function of age), together with our original approach, in the main figure.\nWe think they provide complementary and consistent lines of support for our conclusions - and we thank\nthe reviewer again for suggesting this additional validation method in the first place, which strengthens\nthe robustness of our findings!\nThe aDMS PCA (page 17 of the response) is interesting but should be labelled by age (or decade). Have the\n4 outliers in this PCA (top right) been excluded from subsequent analyses? I would also suggest showing a\nPCA of all loci with decent coverage before showing the aDMS PCA.\n5 of 11\nNCOMMS-25-30818A\nWe have updated this figure to include age labels for each bird, which clarify the relationship between the\nPCA positions and chronological age. Additionally, we now present both PCA analyses with the entire\nmethylome (filtered for coverage as explained in the main methods, panel A), and aDMS-only (panel B),\nallowing for clearer comparison. The 4 “outliers” visible on panel B are actually the 4 young birds that are\nalso clearly apparent on Fig. 1A of the manuscript. In regard to aDMS PC1 (panel B), these are actually not\noutliers stricto sensu: their position is as expected given the age distribution, and very consistent with\ntheir average methylation at aDMS (see Fig. 1C in the main text). Thus, they have not been excluded from\nany analysis. We acknowledge a sampling gap in the wild birds between approximately 1 and 2.5 years of\nage corresponding to the juvenile “wandering years”, when birds are typically absent from the colony. In\nthe zoo, these ages could not be sampled at all due to a lack of recent births at the time of the\nexperiment.\nDoes an “unselected” PCA show effects of aging/zoo etc.?\nIt does indeed: this effect was shown on Fig. S6E of the previous version of this manuscript and\ncommented in the accompanying text. Briefly, the first PC of a whole-methylome PCA reflects both age\nand origin (linear model: ΔAICwith the null model: 33.8, p-value for the “origin” factor=1.07x10-8), but only\nexplains a limited amount of the total variance (4.90%). As we noted there, however, “we underline that in\nneither cases a principal component is guaranteed to covary with age (this is not e.g. an RDA), and PC1 is\nextremely likely to carry other signals than age.”\nResponses to other issues raised are appropriate.\nReviewer #4 (Remarks to the Author):\nThe authors have clearly and satisfactorily addressed all of the comments I raised in the previous round of\nreview.\nWe thank the reviewer for their kind words!\n6 of 11\nNCOMMS-25-30818A\nReviewer #5 (Remarks to the Author):\nTo the Authors,\nThank you for your diligent work and for the detailed responses to the reviewer's comments. I have\ncarefully considered your explanations, particularly regarding the interpretation of epigenetic age\nacceleration (EAA) and your methodological validations. While I appreciate the effort, I remain\nunconvinced by certain aspects, and I believe further clarification and additional data are essential to\nfully support your conclusions.\nMy primary reservations revolve around three key areas:\n1. Interpretation of Intercept-Only Differences in Epigenetic Age: You propose that the observed intercept\ndifference, rather than a slope difference, aligns with a logarithmic model where a constant acceleration\nfactor manifests as an intercept shift. However, my concern persists regarding its biological interpretation\nwithin the same species under different conditions. If a true and sustained difference in the rate of\nbiological aging exists due to lifestyle, it should fundamentally lead to a divergence in aging trajectories,\nreflected as a slope difference over time. The parallel lines, even if mathematically consistent with a\nlogarithmic model, suggest a baseline offset established early, raising strong suspicions of subtle,\nuncaptured batch effects related to sample origin or handling, despite your rigorous efforts in sample\ndistribution and covariate adjustment.\nWe thank the reviewer for raising this crucial point. Although we agree it runs counter to intuition,\nsustained differences in the rate of biological ageing should not lead to slope differences over time under\nthe logarithmic ageing model (i.e. under the model where epigenetic age changes by a fixed amount for\neach doubling or other n-ing of chronological age), provided both groups are observed in the same\nchronological age (x-values) range. This divergence would be observed if the rate of acceleration of\nageing, as opposed to the rate of ageing, was different between the two groups.\nWe illustrate this in the figure above: panel A illustrates the simple logarithmic ageing model proposed by\nAlisch et al. 2012, Horvath et al. 2013, and formalised in Snir et al. 2019. Panel E shows the (constant)\nintercept difference between these two curves. Despite the strong optical illusion, the difference\nbetween the two log lines at any given age is constant. It does not increase faster in early life, nor is it\nrequired to be established in early life. In order to follow the log-intercept model, we simply hypothesise\n7 of 11\nNCOMMS-25-30818A\nthat the difference in average ageing rate is approximately constant throughout the follow-up period in\neach group.\nPanels B-D show the more general model where the rate of ageing is itself a function of time (any arbitrary\nfunction is possible - a constant as in A, linear with time as in B, exponential in C, logistic in D - or anything\nelse). In that case, the log curves can indeed diverge: in the linear acceleration case shown here (as in any\nother monotonous acceleration), the difference between the groups indeed increases with time (panels\nF-H). It is not impossible that this more general model would actually be selected with a much larger\ndataset, especially if it involved e.g. a small linear rate increase (the B case). In our case, it is rejected by\nAIC - but it would not be contradictory with our findings. Here, we simply suggest that the log-intercept\nparameter accounts for most of the observed variance, and that in comparison with it, the difference in\naverage slope is too small to be accurately fitted in a dataset of “only” 64 individuals.\nIn the edge case where that arbitrary rate function is the exponential (panel C), we indeed would revert\nback to diverging lines, i.e. to the linear model of ageing. The difference between groups would increase\nlinearly (panel G). Thus, the linear model can actually be understood as an extreme edge case of the\nlogarithmic model, under which the fundamental measure of time remains logarithmic (each doubling of\nlife-time marks a unit of ageing) but the rate of ageing increases exponentially.\nNaturally, these observations only hold if epigenetic ageing is indeed logarithmic with time - but the fit of\nour data is rather unambiguous here. Importantly, we refer to the “smoke test” included in our study. In\nthis case, smoking is not an early-life stressor, and the subjects included in the study were current\nsmokers or current non-smokers. The stressor (tobacco) is maintained for an extended period whose\nduration is not included in the model. In that case too, this results in parallel EA lines (Sup. Fig. 7): yet it is\ndifficult to argue that this is the result of a batch effect or of an unmeasured early life stressor, and not\nsimply of tobacco smoking. This case is well represented as the logistic acceleration model (panels D and\nH): ageing rate is initially very similar between groups, but increases sharply in the stressed group when\nthe stress (e.g. tobacco use) begins (the curve divergence period), and settles at a higher value. When the\nstressor is stable, the logarithmic curves are parallel again (panel H).\nIn summary, we do not suggest there is no variation (acceleration) in ageing rates in either of the two\ngroups. We simply state that we do not observe this variation in our sample (possibly because it is too\nsmall to be fitted here), and that this is not contradictory with our conclusions. In fact, this represents the\n“null model” where ageing rate difference is close to constant over the observation period. More\ncomplex models could definitely be explored in the future with the appropriate (longitudinal)\nexperimental design!\n2. Lack of Early-Life Data and Implications for Non-Linear Analysis: Your acknowledgment that the\nlogarithmic approximation \"is not correct for very early life\" and that \"these early ages are not sampled at\nall at the zoo\" is a critical point. If the intercept difference is indeed a result of rapid initial acceleration in\nearly development, then the most crucial data for observing and accurately modeling this phenomenon is\nmissing. Without epigenetic data from very young animals in both environments, any non-linear analysis\nof aging trajectories remains speculative. This limits definitive conclusions about the precise timing and\nimpact of early-life lifestyle factors on epigenetic aging.\nWe entirely agree. However, here, we do not draw any conclusions about the precise timing and impact of\nearly-life factors, nor do we suggest that the difference in ageing rate observed in adulthood is the result\nof early life factors. If we were to speculate, we would lean for model D in the figure above, with a gradual\nestablishment of ageing rate difference in the first years of life, as lifestyle differences will be more marked\nfrom fledging onward, when wild birds would start to actively swim in the open ocean before starting the\nbreeding life (and associated fasting), while zoo birds remain sedentary and well fed. But this would not\nmean that the difference is a result of early life events. It would mean that the difference starts to occur\nduring or after early life. This is a key difference, and best exemplified here again by the smoker test: the\n8 of 11\nNCOMMS-25-30818A\nparallel curves observed in adulthood in Supplementary Figure 8A are not a result of whatever happened\nbefore the smoking, but of the ongoing difference in smoking itself.\nWe would also like to nuance the idea that the logarithmic approximation is not correct for very early life.\nOur point was that the logarithmic approximation is correct, but that our representation of the\nlogarithmic curve by a linear one is probably not accurate for the very early life stages.\nWe also agree that studying early life effects would be fascinating. This would involve dense longitudinal\nsampling in a sufficient number of chicks from hatching onward, both at zoos and in the wild. While this is\nclearly outside the scope of this study, this would indeed yield fascinating insights into early life\ndeterminants of age acceleration!\nWe have clarified these points in the manuscript at lines 311-316: “This study has three additional\nmethodological limitations: first, we focus mainly on adult, breeding-age birds. Thus, we are not able to\nexamine whether the apparent difference between wild and zoo-housed birds is established already in early\nlife, or appears gradually. While the intercept difference between the two groups (Fig. 1A) is very consistent\nwith logarithmic EA in presence of a stable age-accelerating stressor (as developed in Supplementary\nMethods S4), we cannot exclude strong effects of early-life rearing conditions.”\n3. Clarity of Training and Test Sets: I find the explanation regarding the training and testing of your\nepigenetic clock model to be insufficient. While leave-one-out cross-validation (LOOCV) is a valuable\ninternal validation technique for assessing model performance within a given dataset, it does not\nsubstitute for a truly independent, external test set. Without demonstrating the model's predictive power\non a completely unseen and separate dataset (e.g., new samples collected independently), the analysis,\nparticularly the significance of the age acceleration plots, remains less convincing. Furthermore, a shared\ntraining set might obscure a true difference across these groups; a more revealing approach might\ninvolve training a clock exclusively on either the zoo or wild samples and then applying it to the other group.\nIt is imperative to clearly delineate the training and test sets used, and if a fully independent external test set\nwas not employed for the penguin data, this should be explicitly stated as a limitation.\nWe agree with the reviewer that adding additional groups to this study would have been ideal.\nUnfortunately, there are also some necessary practical trade-offs that prevent the acquisition of an\nunlimited number of samples. However, training the clock on one group only and predicting for the other\ngroup, as suggested by the reviewer, is one way to alleviate this: it also robustly supports our conclusions.\nWe show the result of this test as a new Supplementary figure 7, reproduced here below.\nBriefly, we used glmnet to fit an elastic net model to our aDMS PCA coordinates, using LOOCV (as in our\nmain analysis), but using only half of the birds to train the model: either zoo birds only (A) or wild birds\nonly (B). Each time, the other group was predicted from that model. We show the predicted values\n(“Epigenetic age”) regressed against the chronological age, together with the coefficients of the\ncorresponding linear model (EA ~ age + origin). The null model is simply EA ~ age. In this case, the\nintercept difference for origin is fully absent from the training data, and is only inferred when regressing\nthe predicted values against age.\nIn both cases, estimates of age acceleration are well supported by AIC, strongly significant, and larger\nthan in the mean-aDMS approach. Training on zoo birds only yields a value close to our original estimate\n(6.00 vs 6.48 years), and training on wild birds only yields an intermediate value (3.83 years). However,\nwhile this approach provides more independent support for our conclusions, we underline the fact that it\nrelies on a halved sample size for model training, and is likely to produce noisier coefficient values - this\nmotivated our initial choice of methods.\n9 of 11\nNCOMMS-25-30818A\nWe have now mentioned this additional validation in the main text at lines 128-133, and to our\nSupplementary methods (lines “Additional validations - c” and Supplementary Figure 7).\nWe also now explicitly stated this limitation point of debate:\n“The numerical differences between these approaches may be explained by different sensitivities (training\nsample size is halved in the first of these controls, and the second one is based a cruder averaging\nprocedure that gives equal weights to all included aDMS CpGs, regardless of the strength of their actual\ncovariance with age). The true value of the age acceleration at the zoo is thus likely between 2.63 years (the\nmost conservative estimate) and 6.48 (the estimate derived from a PCA of the whole sample set) - in any\ncase, we reach the conclusion that zoo-housed birds are significantly age-accelerated compared to their\nwild counterparts.”\nRegarding the delineation of training and test sets in our original analysis, our manuscripts states that\n“For each grid value, we performed a leave-one-out fit: the age of zoo individuals was first transformed\nlinearly using the local slope and intercept, and, taking each sample out in turn, we trained an elastic net\nmodel using all principal components of methylation variance using N-fold internal cross-validation on the\n63 remaining samples. We then used this model to predict epigenetic age for the 64th sample”. This is a full\ndescription of our training / test design: for each point, the other 63 points are the training set. We\nunderline that this is independent from the LOOCV procedure used to train the model on these 63 points.\nWe have now added an additional clarification to our methods at lines 405-406, immediately after the\nnote cited here: “In other words, for each point, the other 63 points are the training set, and LOOCV is\nperformed among these 63 training points, before predicting EA for the 64th point.”\nIn conclusion, while I commend the innovative approach of using King penguins as a model, these points\nneed critical attention. I strongly recommend providing explicit clarification and transparency regarding\nthe training and test sets used for the penguin epigenetic clock, and generating and incorporating\nepigenetic data from very young animals (birth to early developmental stages) from both wild and zoo\npopulations. This is crucial for a robust non-linear analysis and to definitively support your interpretation\nof age acceleration. Until these fundamental data gaps and methodological clarifications are addressed,\ndefinitive comments on the causal relationship between lifestyle and epigenetic age acceleration remain\npremature and potentially an overstatement.\nWe hope that this revised version alleviates these concerns. We agree with the reviewer that studying\nearly life stages at high resolution will be a fascinating and highly informative endeavour, and will likely\n10 of 11\nNCOMMS-25-30818A\nconstitute a complete follow-up project. At this stage, this remains challenging at the zoo (fecundity rates\nare low and it would take years to gather a sufficient sample size, which precludes gathering such data\nwithin the framework of this review process). However, we hope we made it clear now that we do not\ndraw any conclusions regarding non-linearity in early age in this study. We thank the reviewer for their\nconstructive suggestions that have allowed us to provide additional and independent support for our\nresults!\n11 of 11"}]

Decision letter