I went through the manuscript several times for this second round of reviews and the manuscript looks very good to me now. The authors have taken into account most of reviewer’s comment and I am happy with the replies they provided to my own comments. They actually did a great job since criticisms had been raised concerning the phylogeny. The authors have now proposed two different time-calibrated tree that seem to be well done and re-analysed everything with these two phylogenies. The phylogeny is indeed poorly resolved and the authors “grafted” species not sequenced but they largely took into account this uncertainty in the analyses. Hence, to my opinion the results are strong and the well discussed in the light of the recent Pleistocene climate changes.

I just spotted a few mistakes:

Line 436: “were not significant” L463: “regression” L518-519: maybe make more reference to the figures and table, in general for the discussion. L545: “interpreted in the light”?

The manuscript entitled “Pleistocene climate change and the formation of regional species pools” seeks to statistically identify distinct biogeographic regions within the Palearctic region, focusing on the genus Carabus (Coleoptera), in order to test which variables explain best the species turnover across these regions, and whether they fit with the hypothesis the Pleistocene climatic variation affected the pattern of diversity. The authors focus on four (actually three) explanatory variables: i) the ecological niche (climatic niche + habitat), ii) geographic connectivity among regions and iii) phylogenetic relationships. The study does not bring new data and rely on sequences publicly available and distribution data from previous publications of the same authors. Globally, while the Material and Method section and the Results are well written, clear and concise, I found that the Introduction and Discussion are much more difficult to follow, some ideas would require to be better explained, in particular when tightly related to the hypotheses (see below). I really like the approach chosen to identify the biogeographic regions. It gives a real statistical support for describing the pattern of diversity. However, I have more questions about the method used for reconstructing the phylogeny and interpretation of the ancestral range estimation (see details below).

Introduction L33. I find “determine” too strong. Also I am not sure about this sentence and the whole idea of this introductory paragraph. The authors cite for example Ricklefs & He (2016) as an example supporting the idea that “regional biota […] determine ecological and evolutionary processes […] at finer scale”. But the reference above actually supports the idea that the PROCESSES acting at large scale and structuring the regional biota (speciation, extinction, dispersion) can affect local processes. This may sound like a detail but otherwise I do not see how the “regions biota” per se can affect local processes. I also think this clarification is extremely important since the conclusion of the paper (the last sentence) directly refers to this question of PROCESSES acting at large scale and potentially indirectly affecting the local scale. L55-59. I find these two sentences contradictory. Do the authors mean that it is well known that species/population ranges are the result of Pleistocene climate but we do not know how general this is? These sentences should be clarified. L.67-82. This part deserves to be clarified. It gives the framework of the study, and many of the patterns tested are based on this, yet it is confusing. For example l. 67-70, I do not understand the last part of the sentence. I don’t know if this may help but a way of presenting some of the processes would be to talk about the balance (or ratio) between speciation and dispersal/adaption for a region. Variations in this ratio may be mediated by important barriers to dispersal (reducing dispersal) or climatic fluctuations (increasing dispersal) and lead to phylogenetic clustering or overdispersion. L70-71. Throughout the manuscript the authors use “phylogenetically constraint”. To me this is an over-interpretation of the pattern called phylogenetic signal or phylogenetic conservatism (depending on the definition one wants to use). Using phylogenetic conservatism or signal would make things much more clear I think. Also, it is not the “species’ resemblance” that is conserved but the climatic niche, which leads to a resemblance among closely related species. L85. The authors study the “European Carabus”. Does that mean there are non-european Carabus? In other words, is Carabus endemic to the Palearctic? If not where are the other Carabus in the phylogeny, and how this may affect the results (ancestral range estimation in particular) and interpretation?

L99. “presumed low dispersal capacity”: reference needed, especially since hypothesis H1 at least is based on this statement.

L103. Hypothesis H3. This is a question that came to me several times throughout the paper: do we need the Pleistocene climatic fluctuations to explain that lineages living at higher latitudes are adapted to cold environments? After all, temperatures decreasing toward the poles, one would expect to see lineages adapted to cold environments at higher latitudes compared to the Mediterranean basin. I think the authors should think of a way to distinguish between a “simple” latitudinal gradient effect and the Pleistocene climatic fluctuations.

Material and methods L168-172. I wonder: the authors do not give the sign of the expected correlation. Here, the only hypothesis is a positive correlation between niche distance and phylogenetic distance (leading to a phylogenetic conservatism). However one may expect a negative correlation, i.e. closely related species have very dissimilar niches, a pattern one may expect for example in the case of adaptive radiation. Was the test designed to detect both negative and positive correlations? L195-196. The sentence need to be revised. L215. Should remind what a “node” is here. L239-242. The sentence need to be revised. L256. Is there a specific reason for using kernel smoother instead of “polygons”? L287-296. The section about the molecular phylogeny is extremely short and would benefit from adding more information here, instead of simply referring the supporting information. The authors unlink the substitution models in the RAXML across regions (genes I presume) – supposing that each gene follows a different substitution model. However they consider only one clock, estimated only based on the branch length of the RAXML tree and time constraints. I do not understand the choice of using the chonos function for time-calibrating the tree, i.e. using a method that does not even use the molecular matrix to estimate one clock, while this information is available. To me seems like this is under-exploiting the information available. Applying a molecular clock is not simply rescaling a topology based on some constraints. I do not pretend that the results will drastically change but it seems to me like the method used here is quite weak, especially in the context of inferring historical biogeography, where the timing of events is particularly important. L287. Phylogenetic distances were computed from the time-calibrated tree? L323. Ancestral range estimation: Have the authors modified the adjacency matrix or multipliers? Is there a reason for not reducing the adjacent areas?

Results L414. Revise the supporting information numbering. L416. I do not understand which information allows the authors to conclude that colonization occurred “recently”. Because there is no phylogenetic signal? L420. In 59% of cases BAYAREA+j has the lowest AIC. But I am curious, what is the mean AIC difference with the second best model? L422-425. The authors discuss the parameter j. However they do not providing any discussion about the fact that BAYAREA is chosen over other models such as DEC. BAYAREA models speciation event in which both descendant lineages inherit of the entire ancestral range, leading to speciation events that occurred over the entire distribution of the ancestral lineages. How does such model fit when interpreting the results? L419. Concerning the ancestral range estimation: I still think that a short description of the pattern is necessary. I understand that the authors are interested in assessing the role of recent climatic event, but the group is more than 20 my old (according to the phylogeny). I think the authors cannot really ignore the 20 my of diversification before the Pleistocene events. And I would like to see the distribution of species at the tips of the phylogeny, otherwise this information is not available and it will also help better understanding the regional structure. Should we also observe a directional pattern of dispersal events if Pleistocene climatic fluctuations affected speciation and dispersal? Shouldn’t we observe recent northward colonizations? Do we?

Figure 4. Based on this time-calibrated tree, there seems to be parts of the tree that were clearly not affected (at least in terms of speciation) by Pleistocene climate changes. For example the clade including Tomocarabus, Diocarabus, Orinocarabus, Eurycarabus, Aulonocarabus, Pachystus (which is inferred to have occurred in the northern part for a long time) or the clade Archicarabus. Are there any hypotheses that may explain why some lineages have been more affected by Pleistocene climatic events than others?

Discussion L451. Sentence needs to be revised. L451-452. Could be interesting to give an example of how local diversity is affecting to clearly contrast with the result of this paper L460-462. Or simply a lesser geographic complexity? L480-482. Revise the sentence, which in itself cannot be understood. L490-491. Could this also be a consequence of the lower number of species in northern regions? L502. Then vicariant events should be recent; otherwise local diversification would have led to phylogenetic clustering. L516-519. Then where are these founder speciation events in the ancestral state estimation? This statement could be supported by some examples of such events (or event show it on the figure). L522-254. It seems like the authors are still discussing about the +j, but I do not see how this sentence related to the +j parameter. Some rewording is needed.

The paper aims at depicting the processes that contribute to the formation of regional species pools. Using Carabus as a biological model, the authors used a network approach to characterise regional and subregional faunas across Europe. Similarities in species co-occurrence within these faunas were then modelled as a function of climatic niche and habitat similarities, spatial connectivity and phylogenetic distances. I’m not familiar with the analyses used in the paper, but I found the issue very interesting. I think that such studies should enable a better understanding of the origins and dynamics of regional biotas. My main concern was for the structure of the paper. The authors made the effort to define specific hypotheses (H1-H6) in the introduction, which they did not refer hereinafter, especially in the discussion. Moreover, the material and method section is very long. The Data origin section should be embedded in the other subsections for easy readability. If the structure of the paper is revised, I think that it deserves the label of PCI Evol Biol. Minor comments l.69-82: the link between the text and Fig. 1a is not obvious, because the terms used were not the same. Please clarify, or delete reference to Fig. 1a. l. 128: I have not found the map at http://dataservice.eea.europa.eu l. 134-142: the relevance of the environmental and geographical data concerning Carabus could be explained in this paragraph l. 165: “lineages” l. 175: “Further, the independent effects…”: why “independent”? l. 177: “ to geographic isolation (Fig. 1a.iii), whereas…” l. 261-269 were vegetation categories defined at the scale of each grid cell, or more finely? l. 273: “pixel” = grid cell? l. 369-386: what about the geographical consistency of submodules? Please choose between the terms “region/subregion” and “module/submodule” throughout the text to facilitate reading. l. 398-400: spatial connectivity was not significantly related to species co-occurrence in Modules 5 and 6. l. 408-409: “The effects of connectivity were stronger in southern regions (i.e., modules 1 and 3)”: in module 3 it was not stronger than in modules 4 and 7. l. 412-414, “Indeed, niche similarity and spatial connectivity…”: this sentence is confusing and may be deleted. l. 414: “Only niche similarities (mainly climate)”: were all the significant effects of niche similarities among regions and subregions related to climate? l. 415-417: “ as expected if…”: for instance here, the authors should refer more clearly to hypothesis H3. l. 424: “which could be seen as a signal of Pleistocene glaciations…”: or of more ancient events? l. 426 “the range contraction parameter”: named e (extinction) in the Table legend? l. 489: replace “stronger related” by “more strongly related”?

In this study, Catalayud et al. look into how species pools of the genus Carabus are formed in response to Pleistocene climate change. I find the study interesting but I have some issues with parts of the methodology.

I am assuming the methods used to detect species pools and asses the determinants of species pools are sound. I have no expertise in these methods and the section describing them is a little tedious to read and understand.

The matrix design seems a little odd to me. I understand how the matrices are designed but I find it hard for example to understand why the connectivity matrix is designed based on solely topography and presence of water bodies. The slope and the presence of water bodies are not necessarily the most crucial factors determining Carabus beetle dispersal. A more inclusive view would be to take into account ecosystem/niche change/breaks. At the moment, this is decoupled in the different matrices. It is not clear to me if this makes sense in a biological way. Knowing the biology and distribution of Carabus in Western Europe, it is not clear to me why the authors chose the slope and presence of water bodies as proxies for barriers limiting dispersal.

Are the 16S alignments with Kalign and MUSCLE strictly identical? If not I don’t see why the authors mention the use of a criterion to select their alignments under different programs. They seem to select a better alignment in MUSCLE but decide to take a suboptimal one based on the criterion that they decided to use in the first place.

The phylogenetic and dating analyses could be improved. The dataset was not partitioned and was analyzed as a whole. This is most likely suboptimal. Furthermore, the backbone of the topology was constrained to reflect the one of Deuve et al. (2012). I don’t see a good rationale to do so, especially considering the rather low nodal support across Deuve et al.’s topology in the first place. The dating is equally odd, with no less than 21 secondary calibrations used to date the resulting RAxML topology. I am wondering why the authors did not directly use the chronogram from Deuve et al. and pruned the tips they were not interested in.

It should be added that the dating of Carabus origin is debated even though the literature shows at the moment a unique hypothesis (e.g. several studies by Andujar and colleagues). The latest dating of the beetle-tree-of-life (McKenna et al. 2015; Toussaint et al. 2017) clearly show that Carabinae split from Trachypachidae >150 million years ago. Based on this extremely old divergence, it seems unreasonable to assume an age for the crown of Carabinae at <50 Ma. Most dating studies focusing on Cychrini or Carabini have been based on substitution rates of mitochondrial genes or on biogeographical constraints which are well-known to potentially result in dramatically underestimated ages. This should be kept in mind when analyzing divergence times in Carabus and other related lineages. In their results and discussion, the authors mention the perfect fit of their dating and BioGeoBEARS analyses with the Pleistocene glaciations, emphasizing confidence intervals of tens of thousands of years. This is likely not conservative and could be highly biased considering how shaky the divergence times estimates within Carabus are likely to be.

The placement of taxa based on “taxonomic knowledge” is somewhat dubious and I am having a hard time understanding it. I am not really convinced by the method developed in Rangel et al. (2015). The phylogeny of Carabus is complex and the morphological affinity among species of certain groups has been largely challenged by molecular data in the past decade. Here, the authors place >30% of the species they study in clades of the (moderately to poorly supported) tree based on “taxonomic knowledge”. This is not really appropriate in the absence of proper morphological justification, and all analyses based on the resulting topology are likely to be severely biased.

Overall, I feel that the topic of this study is important. Some results are very interesting, such as the grouping of 7 zoogeographical regions and the importance of niche similarity and spatial connectivity in shaping the co-occurrence of species. The different impact of factors in Northern and Southern regions is also very interesting. But I also find that while the authors use quite complicated methods, they pay less attention, to some extent, to the crucial steps required to build either their models (matrices) or datasets (phylogenetic tree and chronogram). They also barely mention any bias or a more balanced view that could originate from their results. For instance, the result that phylogenetic distances were not correlated with regional co-occurrence is likely biased by the suboptimal methodology used to build a chronogram in this study. Similarly, the authors are quite speculative in their discussion but seem to systematically not report any lack of statistical support or confidence intervals. For instance, they disregard the overall complete lack of nodal support in their phylogenetic tree (this is not even mentioned in the text, and not indicated in Fig. 4). The dating analyses are not discussed and there is not confidence interval provided. The likelihood of the BioGeoBEARS analyses is not given. The pattern presented in Fig 4 is one among 100 and has almost no resolution, this might be worth discussing. A final note is the absence of discussion in the context of existing literature regarding Pleistocene range contractions/shift, lineage diversification and faunal re-assembly. There is a large amount of studies looking into this topic using different methodologies, mostly derived from population genomics or phylogeography. This input would be interesting to underscore the importance of these new results in the field.