Understanding patterns and drivers of spatial synchrony in population dynamics is an important area of study within ecology, particularly in light of contemporary impacts on population persistence. This manuscript utilizes a large, spatially expansive dataset of great tit populations in Europe to evaluate the patterns and drivers of spatial synchrony in age structure. Interestingly, while they find spatial synchrony in age structure maintained at a reasonably long distance (650 km) they find that synchrony in environmental attributes have minimal utility in describing patterns of synchrony, despite their apparent strength in explaining local variation in age structure. These results suggest that the drivers of spatial synchrony in populations of great tit may be more stochastic and/or complex than reported for other types of species.

Overall, I found this manuscript to be informative, reasonably well structured and within the scope of Ecology Letters. Moreover, I think the application of the quantitative framework for examining patterns of spatial synchrony has the potential to advance studies of metapopulation dynamics. However, I have a number of concerns regarding data analysis and the author’s rationale for using certain estimates of age structure. Generally, I feel that the modifications outlined below would broaden and enhance the presentation of these results for the Ecology Letters audience.

Proportion of juveniles as proxy for age structure
The authors estimate the proportion of juveniles (first-years) to adults (older), despite the noted lifespan of up to 9 years, as their primary response variable for analyses. The rationale for this metric appears to be based on the reproductive potential of great tit peaking at 2.8 years. However, this univariate ratio does not adequately capture age structure, rather it captures the number of new individuals occurring in a population in a given year, either from immigration (regional) or reproduction (local). While this metric is commensurate with the logic of the analyses – the authors explore potentially causal linkages between environmental attributes and tit reproduction, this metric (or 4/5 additional variables described in the supplement) does not describe the inherently multivariate age structure of populations. This is an important attribute of the study, given that capturing variation in age structure can provide meaningful insight into population-level fecundity and persistence, and when assessed through the lens of spatial synchrony can provide information regarding how and when disparate populations are linked. Of the supplementary response variables, mean age temporal deviations may capture this the best, however synchrony analyses were not reported for this variable. I see two potential solutions for this issue:
(1) To acknowledge that proportion of juveniles is only one attribute of age structure and does not capture the multivariate nature [and implications] of age within populations. This would require performing additional analyses on the [mean age temporal deviations] supplementary response variable and perhaps a new response variable that adequately captures multivariate age structure.
(2) Remove "age structure" from the manuscript.

Asynchrony
The authors employ a type of spatial synchrony analyses (sensu Engen et al. 2002) that exclude the possibility of spatial asynchrony (or negative synchrony) of populations and environmental variables (L271-272). Populations have to potential to exhibit positive and negative spatial synchrony at local and regional scales (Wang et al. 2014 Ecology Letters; Wang et al. 2021 Ecology; LaMontagne et al. 2020 Nature Plants). Although asynchrony is largely considered within the context of “asynchrony as a stabilizing force”, it is certainly applicable within the context of simple coherence in population dynamics over space and time. Specifically, negative correlations between biological attributes of spatially distributed populations [and attributes of the environment] can be indicative of important ecological and environmental dynamics. For example, the abundance of bird populations between two locations may exhibit negative correlations over time due spatial patchiness in rainfall, despite the locations being relatively close together, say <100km apart. The prevalence of this effect (i.e., the Moran effect) should increase with distance, however, as the authors accurately note, it is largely driven by the present of environmental variation over space. Although it appears that the analyses performed require the exclusion of negative correlations, their exclusion removes important information from the analyses. There are alternative ways to estimate spatial autocorrelation and synchrony that account for negative correlations and/or asynchrony, is there a particular reason why the authors selected this method, consequently removing the potential for spatial asynchrony to be detected? I disagree that “biological interpretation of biological parameters” is adequate rationale. I expand on why this is an important consideration for a particular manuscript excerpt in the specific comments below.

General comments
-In accordance with the previous point regarding the use of proportion of juveniles as a proxy for “age structure”, not enough credence was provided to supplementary metrics for age structure. As far as I can tell, none of these metrics or associated analyses are described in the main text aside from a brief mention on L184-186 of the methods. If they aren’t important then they shouldn’t be included, however it does appear that they are important to the story and should be acknowledged in the context of the main findings in the manuscript text.

-The authors consider their results in the context of density-dependence throughout the manuscript. This appears to be most relevant when explaining the [strong] effect of clutch size on local proportions of adults:juveniles. However, extending these results to explain density-dependence or alternatively explain these results through the lens of density-dependence presents a challenge given that the analyses do not capture attributes of population size in response variables. I wonder if the authors can provide some text, perhaps around L362-367 where this might be most relevant, to bridge this gap.

• A logical line of thought stemming from these results regards the effect of environmental variables on beech masting. The authors did not find an effect of temperature metrics on synchrony in age structure, but did find a weak effect of beech masting across local populations. What drives the referenced “spatial synchrony in beech masting”? Could the effect of temperature metrics (winter lows, ECEs, etc.) be masked by variation in beech masting – their effect is indirect?

-The conclusion passage should be broadened rather than as a rehash of prior discussion points.

Specific comments
-L107: Revise for clarity: “variation in age structure is fundamentally non-stationary.”

-L120: “if density crashes” should be “if population crashes”?

-L134-135: The causal logic in this line is a big challenging to interpret. It seems backwards to assume that spatial coherence in fluctuations decomposes the mechanisms of coherence. Shouldn’t it be the other way around?

-L135-138: “climate change is increasingly affecting wild populations through survival…” This is fairly broad. Can the authors be more explicit about climate impacts?

-L164-167: Information regarding data collection is very limited and it falls on the reader to find information and metadata for how data and metadata are collected. Methodological detail needs to be expanded significantly here or in the supplement.

-L173: Additional to the previous comment, it is unclear how identity was known for birds. Are these tagged individuals?

-L176-178: This assumption needs a reference.

-L199-200: “population-level average clutch size as the mean number of eggs produced per breeding attempt within a breeding season” – Does this estimate consider the population size at a location?

-L202-211: Environmental variables. The authors expand on the source and handling of environmental variables in the supplement. However, there should be some acknowledgement of the spatial location and/or resolution of collection.

-L214: What is the specific scale of “vary at a large spatial scale”?

-L306-308: “…very weak trend toward smaller proportions of juveniles…”, supported by Figure S3a. This pattern seems very difficult to interpret from this figure. Additionally, it doesn’t appear to be highly relevant to the overall results, such that it should be included in the first paragraph of the results.

-L310: Provide a table reference for this result.

-L338 - revise for clarity: “with XXX, XXX and XXX being the strongest predictors of temporal variation in breeding age structure.”

-L384 to 389: This section is confusing. The main message is that “that cold temperature-driven mortality is non-age-specific, thus reducing local population size across all age-cohort”. The authors appear to be generating multiple hypotheses for why low winter temperatures could result in differential mortality. Perhaps this can be clarified here prior to the main message on L388-389.

-L381 to 403: In addition to the previous comment. This paragraph would benefit from restructuring. The authors aim to decompose the negative effect of low-winter temperatures on the proportion of adults:juveniles (i.e., more juveniles following strong winter). The various mechanisms provided by the authors appear valid, but the argument is not well constructed. Perhaps outlining the specific hypotheses prior to decomposing them within each sentence would clarify the paragraph.

-L432 to 438: The authors provide an explanation as to why age structure (here, proportion of juveniles) was not predicted by environmental variables. They note proximity to stationarity as well as its alternative, chaos, as potential reasons for this. Given that the response variable is a fairly coarse univariate, then constrained to correlations between 0 and 1 (i.e., asynchrony in values prohibited) in analyses, it is not entirely surprising that the predictive capacity of this approach was limited. Consideration of (1) the inherent multivariate nature of age structure and (2) the potential of asynchronous dynamics may assist in decomposing this complexity. Although the later may lead to greater variation in correlations and potentially poorer model fit, ignoring it fails to consider the very distinct possibility of asynchrony between regional and even local populations. For example, there may be some spatial threshold at which beech masting becomes asynchronous which is mirrored by tit population dynamics. In short, I am not convinced that excluding negative correlations from these analyses is the proper procedure for examining these dynamics.

-Figure 3: Provide color legend inside plot.

-Figure S2: Need to better define facet labels, add axis titles. Are these estimates normalized, what are the units?

Understanding patterns and drivers of spatial synchrony in population dynamics is an important area of study within ecology, particularly in light of contemporary impacts on population persistence. This manuscript utilizes a large, spatially expansive dataset of great tit populations in Europe to evaluate the patterns and drivers of spatial synchrony in age structure. Interestingly, while they find spatial synchrony in age structure is maintained at a reasonably long distance (650 km) they find that synchrony in environmental attributes have minimal utility in describing patterns of synchrony, despite their apparent strength in explaining local variation in age structure. These results suggest that the drivers of spatial synchrony in populations of great tit may be more stochastic than reported for other types of species.

This is my second review of this manuscript. The revised version of this manuscript is much improved and the authors have enhanced the description of the methods and analyses, and interpretation of the resulting patterns. In particular, the expansion of the supplementary materials describing data acquisition and of the performance of alternative response metrics for examining spatial synchrony in great tit population dynamics has enhanced the interpretability and repeatability of this research.

As in my previous comments, I still have two general but important lingering concerns regarding (1) the use of the term “age structure” to describe the primary response variable explored here, and (2) the exclusion of negative synchrony from models. I expand on these items in greater detail below.

Regarding age structure
The authors’ rationale for keeping the proportion of juveniles to adults as the primary response variable is sound in accordance with the general logic of the analyses, as previously noted. However, I am still unsure about referring to this ratio as ‘age structure’, which is not a univariate attribute of populations. There are a number of individual and population-level processes that are influenced by age (e.g., fecundity, growth) often in a non-linear capacity. For example, in many marine fishes the average fecundity of individuals increases with both age and size (Winemiller and Rose 1992, DOI: 10.1139/f92-242). Age-dependent dynamics are also regulated by density-dependent processes (e.g., number of males in a population). For example, it is seemingly possible that 3 and 4 year-old tits differ in for example, maternal provisioning of offspring. In this example, the current analyses suggest that the difference between juveniles (1 year) and adults (<2 year) is greater than the difference between 3 and 4 year adults. While this may be indeed true, the current design makes assumptions about these population-level processes (i.e., all adults over a certain age are effectively the same). Indeed, Gamelon et al. (2016 Ecology) note that the contribution of individual great tit to density regulation depends on age: the youngest age class (1 year olds) is the ‘critical age group’ and fecundity decreases with age.
I don’t see the chosen response variable (juveniles: adults) as a flaw in this design given the population dynamics of great tit and the hypotheses tested. Rather, I see the terminology (i.e., ‘age structure’) as an issue. Age structure is inherently multivariate (Caswell, H. 1989, Matrix Population Models: Construction, Analysis, and Interpretation) and the proportional response variable described here is not. This may seem semantic; however, given the novelty and importance of this study—we know little about the spatial synchrony of population demographics—and its potential consideration for Ecology Letters, it is important to consider the scholarship that may result from an overly simplistic view of population age structure. At the minimum, the importance of this distinction should be highlighted in more detail in the justification provided on L183-186.

Exclusion of asynchrony
I understand the authors’ quantitative rationale for proceeding with the current approach that excludes spatial asynchrony: the extraction of estimated parameters for comparison with other studies. However, I am still concerned about the exclusion of negative correlations (i.e., asynchrony) from analyses, which seem to be quite apparent in the study system/species (Figure 3A). In Fig. 3A and the concordant figures in the supplement, the modeled line is only being predicted by positive synchrony values, correct? For one, it begs the question: why are those values plotted if they aren’t included in the model—this should be noted in the figure caption. Secondly, if they are included in ‘a’ model would the fit and resulting interpretation differ? For example, if asynchronous dynamics are included in a model, does the spatial scale of synchrony [and fit between the two] decrease?
In order to address this concern, I would suggest comparing the performance and fit of the current model with a model that considers negative correlations. This could be achieved with a General Additive Model, for example, with a spline for space and inclusion of environmental covariates. Although GAMs are semi-parametric, this comparison would provide a general indication of whether there is bias towards positive synchrony.

I thank the authors for their thoughtful consideration of reviewer comments. I feel that the revised version of the manuscript is improved, analyses better described and achieves generality for the Ecology Letters audience.

I look forward to seeing this manuscript in print.