This is a very interesting and conceptually and methodologically impressive study. The authors present a new hypothesis that integrates and reconciles previous ones through a time-variable framework. In agreement with comments in previous revisions, I find the contextualization of the AGE hypothesis to be excellent, including also testable predictions from other hypotheses (such as those ones presented in table 1). In my opinion, this synthesis in its own deserves credits enough as to make an important contribution to the LDG field. In this line of merits, the authors used a throughout methodological approach to test predictions from the AGE hypothesis, including three taxa and phylogenetic (SSE models and DEC), fossil informed phylogenetic (DEC + fossils) and fossil analyses (PyRates). This provides inciting results (such as the disagreement between fossil and phylogenetic analyses), which again in its own may have an important impact on biogeographical and comparative studies. Overall, I find the study very interesting and I appreciate the outstanding synthetic and analytical effort behind it.

While I really like the manuscript as it is now, in my opinion there are few minor aspects that could be further improved. Nevertheless, it is worth noticing that I’m just a short-experience practitioner on some of the analyses used. Thus, I can not deeply evaluate the adequacy of some analyses and especially those based on fossils.

1)Perhaps the most important thing is that results in general could be presented in a more informative way. That is, while I like the figures and appreciate the effort to synthetize results from all taxa and type of analyses, I feel that important piece of information are lacking or at least difficult to access. For instance, credibility intervals in figs. 4 and 3 are difficult to visualize, especially for diversification rates. In my opinion the manuscript would benefit from presenting credibility intervals where they were computed (i.e. SSE and PyRates analyses) numerically (e.g. in Table 2). I think this is quite important to clearly demonstrate that the results support predictions from the AGE hypothesis. For instance, in fig. 4, it seems to me that the credibility intervals of diversification rates in the Holarctic and Equator datasets overlap (at least for turtles). If so, the crucial statement of lines 322-325 (i.e. “the slowing of diversification was much stronger in the Holarctic than at the equator”) would be weakly supported and perhaps some rewording would be needed.

2) If I understand properly, during ancestral range estimation analyses the number of dispersal and range extinction events are calculated based on the most probable node state. While this seems to be a commonly used procedure, I think it ignores that the most probable state of a given node can still present a low probability. In others words, the uncertainty inherently associated to the model is not considered as the node state is taken as certain. As the node state probability is not provided it is difficult to evaluate whether this may influence subsequent estimations on the number of “into the equator” and “out of the equator” dispersal events. At first glance and for instance, this may be overcome by calculating the probability that such events occur for each phylogenetic branch. Then, these probabilities could be used along with any resampling technique to estimate the number of dispersal and range contraction events as well as its confidence. Please, forgive if I’m wrong and take this with caution since I’m not an expert in this sort of approaches. Alternatively, I think the state node probabilities should be provided and caution should be taken if these probabilities are low.

3) I do not understand very well why the number of dispersal events are normalized by the number of lineages. To my understanding by doing so results cannot be longer related to diversity patterns (as diversity is being controlled for).

4) From the complete ignorance, is it possible that some incongruences between phylogenetic and fossil evidence come from the different taxonomic level used (i.e. species vs genus, respectively)?

5) It seems that supplementary figures are mislabelled (e.g. those referred in lines 265-268)

6) In line 530 I think it should be “23/34”.

7) In my opinion lines 604-606 should be in the results or discussion sections (right now it is only discussed for the group apparently not following the first AGE postulate, which seems unfair).

The present manuscript by Meseguer and Condamine address and interesting and complex question using different approaches. The present version looks to be quite mature, well written and structured. Authors discussed general patterns explaining the Latitudinal Diversity Gradient in a scenario of Asymmetric Gradient of Extinction. They discussed all different results from each analysis instead choosing “the best” option to explain their hypotheses. This keep in some cases open conclusions, which is in my opinion, a positive thing considering the methodological complexity of the analyses in the manuscript and the assumptions that are implied on each one, which makes difficult to choose one alternative over the others. They also present ancestral area reconstructions with, and without fossil records in the analyses, comparing both results, again, without choosing one over the other.

Nevertheless, I found some methodological aspects that must be, at least, discussed and better justified:

In Methods, lines 594 to 594, authors assume that “taxa inhabiting the warm Holarctic were adapted to tropical-like conditions”. This assumption is supported by a reference for turtles (Testudines) but not for Squamata nor Crocodilia. You must include at least some references supporting this assumption for these two groups as in Testudines, to justify it before performing the analyses.

Additionally, authors used a DEC model for their biogeographical analyses without any specific motivation (at least it is not specified in the manuscript). Why are you using this model and no alternatives like a DIVA or BayArea-like? I would like to see some justification for the use of this model in your analyses. On the other hand, I am concerned about using fossils in a comparative study for the Holarctic and tropical regions. Fossil preservation is different in both cases due mainly to different climatic conditions. This led to a different number of occurrences (fossilization is easier to occurs in Holarctic regions), which can bias the analysis in PyRate due to lack of information in tropical regions.

Finally, in figure 7 caption, I would specify that black line corresponds to the temperature for an easier interpretation of this figure.

See the attached document with the recommender's comments

This is a very nice piece, trying to provide more realistic models of the macroevolutionary processes that drive latitudinal gradients of diversity on Earth. As such, models provide a bold approach to model extinctions and dispersions between latitudinal bands, accounting for long-term climatic oscillations. The modelling part seems sound to me, although I am just a well-informed reader rather than an expert in that part. But the main hypotheses behind the models provide an incomplete coverage of Latitudinal Diversity Gradients (LDGs), and the data itself has some limitations that have not been accounted for, or at least discussed.

You state explicitly along the whole text that the Latitudinal Diversity Gradient (LDG) is universally a decrease from richer tropics to less diverse temperate and, progressively, polar regions. This is far from being an absolute truth. I can concur that such LDG stands out for many biological groups (reptiles are certainly one of these groups), but a large number of taxa and functionally-consistent groups show other LDG patterns. Besides the typical textbook examples of, say, penguins (that are just a small clade and therefore not suitable for your coarse-evolutionary extent model), there are many groups that present their maximum diversity peaks at the temperate zones, including grasses, conifers, bryophytes, many groups of freshwater invertebrates (e.g. dive beetles, trichopterans, plecopterans, ephemeropterans, etc.; Vinson & Hawkins Ecography 2003; Boyero & Pearson J N Am Benthol Soc 2009; Morinière et al. Sci Rep 2016), parasitoid wasps, aphids (Kouli et al. Ann Zool Fennici 1994), certain families of dung beetles (but not others), among many other examples. These groups encompass a large part of terrestrial biodiversity (there are more known dung beetle species than birds and mammals altogether, for example). Patterns in the marine environment are also heterogeneous, and for many groups correlate more with the distribution of upwelling sources than with latitude. So there are many inverse LDGs due to the constraints imposed by their bauplans (see Kindlmann et al. in Scaling Biodiversity, ed. Storch et al., 2007). These basal bauplans (i.e. structural plans) are a direct consequence of the origin of each one of these major clades, that does not correspond to warm tropical periods and/or equatorial origins (e.g., the evolution of mosses in the Ordovician Ice Age, the clades originated in Laurasia during the Carboniferous, the C3/C4 transition in the Miocene and the adaptation of the major grass clades to arid and seasonal environments, etc.). Turtles show some deviation to the classic tropical-peak LDG pattern, but I miss any reference on how this affects the observed LDG for them in the context of your model.

Does this affect the validity of your alternative model? I do not think so, but questions its generality. I do think that it is has the potential to provide a nice representation (but see below) of the patterns and processes followed by many groups that currently show apparent “tropical niche conservatism” patterns. In fact, that physiological limits rather than dispersal limitations shape the patterns of diversity for many groups in the interglacials seems more than reasonable, and many groups may follow that pattern, but sometimes these patterns are mediated by other requirements, promoting peaks of diversity at higher latitudes. Compare, for example, Hortal et al. Ecol Lett 2011 with Calatayud et al. J Biogeogr 2017; I quote these because I know them well, but they show how the same processes with different basal adaptations to climate lead to contrasting latitudinal patters (within Europe in this case). In what respects to recovering the LDG, your model only applies to taxa evolved in warm-tropical environments; and it works for reptiles (which are are certainly a warm-adapted taxon). But I wonder if it could be generalized to origins in other latitudinal bands. The processes are certainly there, it may be only a matter of constructing alternative hypotheses for groups generated in cooler moments/regions, where taxa retain “memory” of the conditions where they appeared. I honestly think this would make a great paper. Should you decide not to incorporate this into the models, the partial character of the richer-in-the-tropics LDG should be acknowledged throughout the text, making clear that your models seek to represent LDGs centered around the equator.

Apart from that, I miss an assessment of whether your results are flawed by eventual biases in the fossil record. It is well known that we lack enough fossil data and adequate models to represent the tree of life, what has been termed the Darwinian shortfall (Diniz-Filho et al. TREE 2013; Hortal et al. Ann Rev Ecol Evol Syst 2015). So it is really hard to buy the assumption that the fossil record is complete; should it be unbiased, I could live with it, assuming random error and undersampling of the tree. But there is a high chance that biases in the fossil record affect the results of your paper. In this particular case, most neotropical palaeontologists advise about the strong taphonomic bias towards the Holarctic; fossils are scant in tropical regions, in part because lack of paleontological effort, and in part due to the lower adequacy for the formation of deposits in many of the old soils of tropical South America, which is the continent I know better in this aspect. I’m not so sure about other tropical regions, but my guess is that only Chinese territories hold a comparable sampling effort in tropical Asia. The problem with the comparative oversampling of the Holarctic is that it spuriously increases the probability of finding dispersions into the tropics, compared to out of the tropics (for the Holarctic branches of the tree are more populated). There may be other more sophisticated ways I’m not aware of (perhaps adding probability of fossilization as a prior), but an straightforward way to account for this would be to resample n times the fossils to obtain samples with the same number of fossils in each latitudinal band (or at least, in tropics and Holarctic), and redo the trees n times. This sensitivity analysis (or a Bayesian alternative based on an adequate prior) will provide more robust results. In any case, a fair assessment and/or statement of how the limitations of the fossil record may affect your results is needed.

Besides these two major concerns, the manuscript is nice, well-written and clear. As a minor comment, I’d move the sentences in lines 232-236 to the paragraph starting in line 153. There are perhaps too many figures for an standard paper, but that is a matter of the journal you aim to send it to.

My own biases are obvious in this review, particularly in what respects to being picky with data quality and completeness, but generalizing current LDGs as holding a general peak of the tropics clashes with my experience, and I’ve seen LDGs for a fair number of groups as author, reviewer and editor, plus teaching LDGs for over ten years. So no matter whether you generalize your model or not, please avoid stating that LDG is universally centered in the equator. It undermines a really superb piece of work.

I hope this helps, Abrazos, Joaquín

This manuscript deals with a hot topic of long standing interest among biogeographers, macroecologists, systematists, among others, that of Latitudinal Diversity Gradient (LDG). Despite it being described long ago, it has been reluctant to exclusive hypotheses ready to be tested beyond correlation. However, this pattern has generated a renewed interest within the biogeographic and macroecological community, as modern tools for reconstructing the past of lineages and the areas where they lived, as well as information on fossils record and distribution, are increasing available.
The merits of the manuscript lie on (1) the consideration of competing hypothesis to those canonical assuming a constant through time higher diversity in the tropics; (2) the application of recent tools to explicitly disentangle the role speciation and extinction, and dispersal (although I would prefer the use of migration, just to avoid confusion with the ecological meaning of the term dispersal); (3) the use of massive data of fossil records for the former aim; and finally (4) integrate all this information in a explicit temporal hypothesis o variation according the tropical-temperate type shift.
Despite I am not an expert on the most recent analytical methods on historical biogeography, the manuscript is thought provoking and deserves to be known by the community. I feel that the hypothesis the authors are launching is falsifiable and thus a number of studies will address it, in the extent there are data set suitable for it.

My comments to specific parts of the study, some of them quite wide across the arguments, follow:

Abstract . No mention is provided to specific temporal setting of the study, despite the wide citation of specific dates throughout the main text.
I is convenient that when mentioning “We studied” (line 35) that in fact the study is widely based on existing published phylogenies, which are refined with additional data (e.g. fossils). This is also applicable to lines 147-149, at the end of Introduction.
My view about the challenge the study represents (line 43) is that in fact the authors propose a refinement of the current theories by incorporating meaningful data on temporal context with independent data (fossils), which might change in the future, when more studies on other groups are available, our views about the LDG.

Introduction
Your approach is to use different groups as to test your hypothesis (three in your study). This brings me two thoughts. One is the selection of groups. Your selection is of three groups which are related, this might limit the power of your analyses. In fact, it would be needed that you mention in the Introduction the rationale for selecting these groups, even thought you justify in detail the Methods section. The reader needs to know somewhat about this as soon as possible. The second is that, independently of the relationships among groups, it recalls about the correlative value of biodiversity patterns in groups. I mean that it should posed the question of the use the patterns in some groups as proxies for general patterns, which in fact is the ultimate aim of the study.
A serious issue throughout the manuscript is the strong bias towards the Northern Hemisphere (Holarctic is included among keywords, but see line 122). Probably this is an effect of the particular distribution of the groups selected. This is not bad at all, but a different selection of groups would have increased the prospective value of the hypothesis, particularly due to the fact that in Southern Hemisphere the climate changes were very probably smoothed due to the sea/land configuration and extension of plates. If the authors are correct, the LDG should vary not only through time, but also through hemispheres.
In table 1 and others there is not indication of the meaning of “r” in the legend. For familiar readers it is clear that this is diversification rate, but should be made explicit.

Results
Line 165. What is the meaning of “region” here? Biogeographical? Any other?
I wonder in what extent results may rely on different rates and probabilities of having reliable fossil records in particular regions (e.g., the tropics). This is central to the whole study. Traits, Ecology...