The submitted manuscript outlines an interesting reciprocal translocation experiment, in which bank vole fecal microbiomes are characterized before and after translocation to/from rural/urban forests. This is a timely study and represents an important experimental step in a field of research which remains largely descriptive. That said, I have struggled to follow the authors’ logic at a handful of intervals and found it difficult to link their assertions to the myriad tables of statistical outputs. Overall, I have a number of concerns that I feel need to be addressed.
Major comments:
1. Plasticity versus resistance: Much of the manuscript is dedicated to testing for plasticity and/or resistance in the microbiome. These patterns are discussed as though they are two alternative patterns that can occur simultaneously or independently. To my understanding, plasticity and resistance opposite ends of a spectrum (i.e., inversely proportional to one another?). Perhaps I am misunderstanding, but I can’t imagine a scenario in which as trait is simultaneously highly plastic and highly resistant. In examining the papers cited, it seems to me the plasticity and resistance describe the same thing, but are terms used in differing fields of research. Evolutionary biologists use plasticity to describe environment-dependent expression of organismal phenotypes (separate from GXE), while community ecologists use resistance to describe the stability of biological communities to perturbation. I would suggest that the authors select one paradigm (microbiome as a trait, or microbiome as a host-associated community) and use either the term ‘plasticity’ or ‘resistance’.
2. Seasonal effects: My current interpretation of L112 is that translocations occurred between July & September 2020. Since voles were re-captured 3-4 weeks after translocation, does this mean that some individuals were captured into late-September or October? Were translocation treatments randomly interspersed throughout this time? I would imagine substantive environmental differences in Finnish forests between the summer and fall, and rural versus urban environments may show different seasonal changes (season x urban/rural interactions). It would seem important to control for possible seasonal effects.
3. Urban versus rural definition: Voles were taken from/introduced to 40 urban/rural forest sites. I think it worthwhile to provide criteria by which urban versus rural sites were delineated. I am sure it is obvious in a qualitative sense to someone in Jyväskylä, but to a naïve reader, it’d be helpful to understand how these sites were determined, and how they differed environmentally. The description in the methods section (L117-L120) seems to suggest that urban and rural forests were environmentally very similar. It is therefore unclear why urban and rural forests are thought to represent different environments from the voles’ perspective (I think this needs greater explanation in the introduction or the methods). Currently, I believe only the post-transfer microbiomes are displayed within ordinations (although I find the figures somewhat confusing to interpret, see below). To that end, I think it is worthwhile to provide ordinations of the pre-translocation microbiome, to demonstrate that clear urban/rural environmental differences exist pre-transfer (stats to that effect are referenced of L233, but a corresponding figure would be helpful). The purpose of creating separate ordinations for pre- and post- transfer microbiomes also confuses me. I would find it helpful to see these samples displayed within the same ordination. Additionally, I would expect to see differential abundance tests which describe the taxa that differ between environments.
4. Statistical confusion: Throughout the results section, I am struggling to link the results from statistical tests with the conclusions reached by the authors. For example, L264 states that the trans-forest transfers did not match the cis-Forest transfers. In inspecting the referenced supplementary tables, I see that the post-translocation microbiome of Urban-to-Rural voles were significantly different from the microbiome of Rural-Forest voles. The authors use this to conclude that these trans-environmental voles had intermediate microbiomes (presumably intermediate between Urban and Rural microbiomes?). Neither trans-environmental experimental group differed from cis-environmental transfers, supporting the idea of an intermediate community state; however, the fact that trans-environmental treatments differed in their post-translocation microbiome suggests that these intermediate states are quite disparate. Another result overlooked in this analysis is that the Urban-Urban and Rural-Rural groups did not have different microbiomes from one another post-translocations (despite there being an urban versus rural signature in the pre-transfer microbiome). In these transfers, the site of origin and site of transfer were the same environment, and so I would have expected the urban versus rural signatures to be maintained. The fact that they were not, suggests that the experimental translocations themselves had an affect, or otherwise that there are strong idiosyncratic differences between sites. I think this result needs some serious consideration.
5. Abundant versus rare: The division between rare and abundant ASVs seems somewhat arbitrary, which I think limits the interpretability. Furthermore, as these taxa are pulled from a compositional pool, they might not necessarily be independent. Because there are many more taxa identified as rare than abundant ASVs (1147 versus 126), it’s not necessarily surprising that this group is more phylogenetically disperse, since you’ve sampled a larger fraction of the community. Additionally, abundance and prevalence tend to go hand-in hand (see Neutrality in the meta-organism), it is therefore unsurprising that no difference in beta-diversity is observed after restricting analyses to abundant taxa, when using a presence/absence distance metric.
6. Stochasticity and dispersal: In the introduction and discussion, plasticity or resistance are described to result from deterministic processes acting in a directional or stabilizing fashion. Stochasticity is also acknowledged briefly in the form to Anna Karenina Principles. In a way, that authors have tested for environment related stochasticity in beta-dispersion tests. In the pre-translocation microbiome, no difference in beta-dispersion is observed between urban versus rural sites, across most diversity metrics. Conversely, urban originating squirrels had more disperse microbiomes post-translocation, across distance metrics. However, this interesting result appears to be largely overlooked, as they don’t feature in the discussion.
Additionally, there is mounting evidence that dispersal is an important ecological mechanism that shapes host-associated microbiomes. However, this mechanism also seems to have been largely overlooked in the submitted manuscript. With that said, how widely spatially distributed were these sampling sites? It occurs to me that despite treating each site as an independent unit, environment type might be partly confounded by an underlying non-random spatial structure. The fact that Urban versus Rural sourced voles differed in their pre-transfer microbiome among bray-curtis analyses but not weighted unifrac analyses suggests that there is not a large phylogenetic (and therefore functional) difference between these communities. These mismatched results strongly hint that dispersal limitation may be a major driver of these patterns.
Minor comments:
-Throughout the results section, I think it worth reiterating which type of statistical test was used at each step of the way. I found myself lost in a flurry of p-values and R2.
-L267: Again, I see plasticity and resistance as the same thing, therefore this r-squared reporting is confusing. What were the actual variables that these values correspond to?
-L285: It’s unclear what this means, since plasticity and resistance are opposite sides of the same coin.
-Figures 4&5: I don’t think there is value in displaying R2 values in a barplot form. Also, in the case of the weighted UniFrac measures, I’ not sure variables can be said to explain X% of variation, if the effect is not statistically significant.
-Figure 3: I don’t understand what the y-axis in this figure represents. Are these values truly a change in beta-diversity (e.g., wUnifrac distance 1 – wUnifrac distance 2)? If so, it’s unclear how these values are derived and what they represent. My guess is that these are simply the distance values between pre and post transfer samples (i.e., beta diversity, not change in beta diversity). If the latter, are these boxplots constrained to pairwise comparisons between the same individual, or between all individuals within the same experimental group? This should be clarified.
-Was the extraction order of samples randomized to prevent batch effects? Or were all samples from a given experimental group processed together?

I would like to commend the authors for completing such an ambitious reciprocal translocation experiment and for considerably revising this manuscript based upon the first set of reviews. I feel the authors have addressed many of the concerns I initially flagged and feel the manuscript i more easily understood in its current iteration.

One remaining concern that I have is the use of linear regression models to complete the analyses detailed in Supplementary Table S6. If I understand correctly, the response variable used are pairwise beta diversity estimates. With this in mind, I would expect considerable non-independence between data points, since any single microbiome sample would contribute to the calculation of multiple beta diversity estimates. I wonder if the dyadic modeling outlined by Raulo et al. (2021)—a paper cited by the authors—could provide more robust estimates.

When reporting PERMANOVA outputs in the main text, I also like to see the F-stat values.