Linking the evolution of two prefrontal brain regions to social and foraging challenges in primates

Reviewer #1 (Public Review):

The present study provides a phylogenetic analysis of the size prefrontal areas in primates, aiming to investigate whether relative size of the rostral prefrontal cortex (frontal pole) and dorsolateral prefrontal cortex volume vary according to known ecological or social variables.

I am very much in favor of the general approach taken in this study. Neuroimaging now allows us to obtain more detailed anatomical data in a much larger range of species than ever before and this study shows the questions that can be asked using these types of data. In general, the study is conducted with care, focusing on anatomical precision in definition of the cortical areas and using appropriate statistical techniques, such as PGLS.

I have read the revised version of the manuscript with interest. I agree with the authors that a focus on ecological vs laboratory variables is a good one, although it might have been useful to reflect that in the title.

I am happy to see that the authors included additional analyses using different definitions of FP and DLPFC in the supplementary material. As I said in my earlier review, the precise delineation of the areas will always be an issue of debate in studies like this, so showing the effects of different decisions in vital.

I am sorry the authors are so dismissive of the idea of looking the models where brain size and area size are directly compared in the model, rather preferring to run separate models on brain size and area size. This seems to me a sensible suggestion.

Similarly, the debate about whether area volume and number of neurons can be equated across the regions is an important one, of which they are a bit dismissive.

Nevertheless, I think this is an important study. I am happy that we are using imaging data to answer more wider phylogenetic questions. Combining detailed anatomy, big data, and phylogenetic statistical frameworks is a important approach.

Reviewer #2 (Public Review):

In the manuscript entitled "Linking the evolution of two prefrontal brain regions to social and foraging challenges in primates" the authors measure the volume of the frontal pole (FP, related to metacognition) and the dorsolateral prefrontal cortex (DLPFC, related to working memory) in 16 primate species to evaluate the influence of socio-ecological factors on the size of these cortical regions. The authors select 11 socio-ecological variables and use a phylogenetic generalized least squares (PGLS) approach to evaluate the joint influence of these socio-ecological variables on the neuro-anatomical variability of FP and DLPFC across the 16 selected primate species; in this way, the authors take into account the phylogenetic relations across primate species in their attempt to discover the the influence of socio-ecological variables on FP and DLPF evolution.

The authors run their studies on brains collected from 1920 to 1970 and preserved in formalin solution. Also, they obtained data from the Mussée National d´Histoire Naturelle in Paris and from the Allen Brain Institute in California. The main findings consist in showing that the volume of the FP, the DLPFC, and the Rest of the Brain (ROB) across the 16 selected primate species is related to three socio-ecological variables: body mass, daily traveled distance, and population density. The authors conclude that metacognition and working memory are critical for foraging in primates and that FP volume is more sensitive to social constraints than DLPFC volume.

The topic addressed in the present manuscript is relevant for understanding human brain evolution from the point of view of primate research, which, unfortunately, is a shrinking field in neuroscience. But the experimental design has two major weak points: the absence of lissencephalic primates among the selected species and the delimitation of FP and DLPFC. Also, a general theoretical and experimental frame linking evolution (phylogeny) and development (ontogeny) is lacking.

Reviewer #3 (Public Review):

This is an interesting manuscript that addresses a longstanding debate in evolutionary biology - whether social or ecological factors are primarily responsible for the evolution of the large human brain. To address this, the authors examine the relationship between the size of two prefrontal regions involved in metacognition and working memory (DLPFC and FP) and socioecological variables across 16 primate species. I recommend major revisions to this manuscript due to: 1) a lack of clarity surrounding model construction; and 2) an inappropriate treatment of the relative importance of different predictors (due to a lack of scaling/normalization of predictor variables prior to analysis).

Author Response

The following is the authors’ response to the original reviews.

Public Reviews:

Reviewer #1 (Public Review):

The present study provides a phylogenetic analysis of the size prefrontal areas in primates, aiming to investigate whether relative size of the rostral prefrontal cortex (frontal pole) and dorsolateral prefrontal cortex volume vary according to known ecological or social variables.

I am very much in favor of the general approach taken in this study. Neuroimaging now allows us to obtain more detailed anatomical data in a much larger range of species than ever before and this study shows the questions that can be asked using these types of data. In general, the study is conducted with care, focusing on anatomical precision in definition of the cortical areas and using appropriate statistical techniques, such as PGLS. That said, there are some points where I feel the authors could have taken their care a bit further and, as a result, inform the community even more about what is in their data.

We thank the reviewer for this globally positive evaluation of our work, and we appreciate the advices to improve our manuscript.

The introduction sets up the contrast of 'ecological' (mostly foraging) and social variables of a primate's life that can be reflected in the relative size of brain regions. This debate is for a large part a relic of the literature and the authors themselves state in a number of places that perhaps the contrast is a bit artificial. I feel that they could go further in this. Social behavior could easily be a solution to foraging problems, making them variables that are not in competition, but simply different levels of explanation. This point has been made in some of the recent work by Robin Dunbar and Susanne Shultz.

Thank you for this constructive comment, and we acknowledge that the contrast between social vs ecological brain is relatively marginal here. Based also on the first remark by reviewer 3, we have reformulated the introduction to emphasize what we think is actually more critical: the link between cognitive functions as defined in laboratory conditions and socio-ecological variables measured in natural conditions. And the fact that here, we use brain measures as a potential tool to relate these laboratory vs natural variables through a common scenario. Also, we were already mentioning the potential interaction between social and foraging processes in the discussion, but we are happy to add a reference to recent studies by S. Shultz and R. Dunbar (2022), which is indeed directly relevant. We thank the reviewer for pointing out this literature.

In a similar vein, the hypotheses of relating frontal pole to 'meta-cognition' and dorsolateral PFC to 'working memory' is a dramatic oversimplification of the complexity of cognitive function and does a disservice to the careful approach of the rest of the manuscript.

We agree that the formulation of which functions we were attributing to the distinct brain regions might not have been clear enough, but the functional relation between frontal pole and metacognition in the one hand, and DLPFC and working memory on the other hand, have been firmly established in the literature, both through laboratory studies and through clinical data. Clearly, no single brain region is necessary and sufficient for any cognitive operation, but decades of neuropsychology have demonstrated the differential implication of distinct brain regions in distinct functions, which is all we mean here. We have made a specific point on that topic in the discussion (cf p. 16). We have also reformulated the introduction to clarify that, even if the relation between these regions and their functions (FP/ metacognition; DLPFC/ working memory) was clear in laboratory conditions, it was not clear whether this mapping could be used for real life conditions. And therefore whether that simplification was somehow justified beyond the lab (and the clinics), and whether these neuro-cognitive concepts could be applied to natural conditions, are indeed critical questions that we wanted to address. The central goal of the present study was precisely to evaluate the extent to which this brain/cognition relation could be used to understand more natural behaviors and functions, and we hope that it appears more clearly now.

One can also question the predicted relationship between frontal pole meta-cognition and social abilities versus foraging, as Passingham and Wise show in their 2012 book that it is frontal pole size that correlates with learning ability-an argument that they used to relate this part of the brain to foraging abilities. I would strongly suggest the authors refrain from using such descriptive terms. Why not simply use the names of the variables actually showing significant correlations with relative size of the areas?

We basically agree with the reviewer, and we acknowledge the lack of clarity in the introduction of the previous manuscript. There were indeed lots of ambiguity in what we were referring to as ‘function’, associated with a given brain region. « Function » referred to way to many things! We have reformulated the introduction not only to clarify the different types of functions that were attributed to distinct brain regions in the literature but also to clarify how this study was addressing the question: by trying to articulate concepts from neuroscience laboratory studies with concepts from behavioral ecology and evolution using intuitive scenarios. We hope that the present version of the introduction makes that point clearer.

The major methodological judgements in this paper are of course in the delineation of the frontal pole and dorsolateral prefrontal cortex. As I said above, I appreciate how carefully the authors describe their anatomical procedure, allowing researchers to replicate and extend their work. They are also careful not to relate their regions of interest to precise cytoarchitectonic areas, as such a claim would be impossible to make without more evidence. That said, there is a judgement call made in using the principal sulcus as a boundary defining landmark for FP in monkeys and the superior frontal sulcus in apes. I do not believe that these sulci are homologous. Indeed, the authors themselves go on to argue that dorsolateral prefrontal cortex, where studied using cytoarchitecture, stretches to the fundus of principal sulcus in monkeys, but all the way to the inferior frontal sulcus in apes. That means that using the fundus of PS is not a good landmark.

We thank the reviewer for his kind remarks on our careful descriptions. But then, it is not clear whether our choice of using the principal sulcus as a boundary for FP in monkeys vs the superior frontal sulcus in apes is actually a judgement call. First, and foremost, there is no clear and unambiguous definition of what should be the boundaries of the FP. By contrast with cytoarchitectonic maps, but clearly this is out of reach here. In humans and great apes we used Bludau et al 2014 (i.e. sup frontal sulcus), and in monkeys, we chose a conservative landmark that eliminated area 9, which is traditionally associated with the DLPFC (Petrides, 2005; Petrides et al, 2012; Semendeferi et al, 2001).

Of course, any definition will attract criticism, so the best solution might be to run the analysis multiple times, using different definitions for the areas, and see how this affects results.

Indeed, functional maps indicate that dorsal part of anterior PFC in monkeys is functionally part of FP. But again, cytoarchitectonic maps also indicate that this part of the brain includes BA 9, which is traditionally associated with DLPFC (Petrides, 2005; Petrides et al, 2012). As already pointed out in the discussion, there is a functional continuum between FP and DLPFC and our goal when using PS as dorsal border was to be very conservative and to exclude the ambiguous area. But we agree with the reviewer that given that this decision is arbitrary, it was worth exploring other definitions of the FP volume. So, we did complete a new analysis with a less conservative definition of the FP, to include this ambiguous dorsal area, and it is now included in the supplementary material. Maybe as expected, including the ambiguous area in the FP volume shifted the relation with socio-ecological variables towards the pattern displayed by the DLPFC (ie the influence of population density decreased). The most parsimonious interpretation of this results is that when extending the border of the FP region to cover a part of the brain which might belong to the DLPFC, or which might be somehow functionally intermediate between the 2, the specific relation of the FP with socio-ecological variables decreases. Thus, even if we agree that it was important to conduct this analysis, we believe that it only confirms the difficulty to identify a clear boundary between FP and DLPFC. Again, we have clearly explained throughout the manuscript that we admit the lack of precision in our definitions of the functional brain regions. In that frame, the conservative option seems more appropriate and for the sake of clarity, the results of the additional analysis of a FP volume that includes the ambiguous area is only included in the supplementary material.

If I understand correctly, the PGLS was run separately for the three brain measure (whole brain, FP, DLPFC). However, given that the measures are so highly correlated, is there an argument for an analysis that allows testing on residuals. In other words, to test effects of relative size of FP and DLPFC over and above brain size?

Generally, using residuals as “data” (or pseudo-data) is not recommended in statistical analyses. Two widely cited references from the ecological literature are:

Garcia-Berthou E. (2001) On the Misuse of Residuals in Ecology: Testing Regression Residuals vs. the Analysis of Covariance. Journal of Animal Ecology, 70 (4): 708-711.

Freckleton RP. (2002). On the misuse of residuals in ecology: regression of residuals vs. multiple regression. Journal of Animal Ecology 71: 542–545. https://doi.org/10.1046/ j.1365-2656.2002.00618.x.

The main reason for this recommendation is that residuals are dependent on the fitted model, and thus on the particular sample under consideration and the eventual significant effects that can be inferred.

In the discussion and introduction, the authors discuss how size of the area is a proxy for number of neurons. However, as shown by Herculano-Houzel, this assumption does not hold across species. Across monkeys and apes, for instance, there is a different in how many neurons can be packed per volume of brain. There is even earlier work from Semendeferi showing how frontal pole especially shows distinct neuron-to-volume ratios.

We appreciate the reviewer’s comment, but the references to Herculano-Houzel that we have in mind do indicate that the assumption is legitimate within primates.

Herculano-Houzel et al (2007) show that the neuronal density of the cortex is well conserved across primate species (but only monkeys were studied). The conclusion of that study is that using volumes as a proxy for number of neurons, as a measure of computational capacity, should be avoided between rodents and primates (and as they showed later, even more so with birds, for which neuronal density is higher). BUT within primates, since neuronal densities are conserved, volume is a good predictor of number of neurons. Gabi et al (2016) provide evidence that the neuronal density of the PFC is well conserved between humans and non-human primates, which implies that including humans and great apes in the comparison is legitimate. In addition, the brain regions included in the analysis presumably include very similar architectonic regions (e.g. BA 10 for FP, BA 9/46 for DLPFC), which also suggests that the neuronal density should be relatively well conserved across species. Altogether, we believe that there is sufficient evidence to support the idea that the volume of a PFC region in primates is a good proxy for the number of neurons in that region, and therefore of its computational capacity.

Semendeferi and colleagues (2001) pointed out some differences in cytoarchitectonic properties across parts of the FP and discussed how these properties could 1) be used to identify area 10 across species 2) be associated with distinct computational properties, with the idea that thicker ‘cell body free’ layers would leave more space for establishing connections (across dendrites and axons). This pioneering work, together with more recent imaging studies on functional connectivity (e.g. Sallet et al, 2013) emphasize the critical contribution of connectivity pattern as a tool for comparative anatomy. But unfortunately, as pointed out in the discussion already, this is currently out of reach for us.

We acknowledge the limitations, and to be fair, the notion of computational capacity itself is hard to define operationally. Based on the work of Herculano-Houzel et al, average density is conserved enough across primates (including humans) to justify our approximation. We have tried to define our regions of interest using both anatomical and functional maps and, thanks to the reviewer’s suggestions, we even tried several ways to segment these regions. Functional maps in macaques and humans do not exactly match cytoarchitectonic maps, presumably because functions rely not only upon the cytoarchitectonics but also on connectivity patterns (e.g. Sallet et al, 2013).

In sum, we appreciate the reviewer’s point but feel that, given the current understanding of brain functions and the relative conservation of neuronal density across primate PFC regions, the volume of a PFC region seems to be reasonable proxy for its number of neurons, and therefore its computational capacity. We have added these points to the discussions, and we hope that the reader will be able to get a fair sense of how legitimate is that position, given the literature.

Overall, I think this is a very valuable approach and the study demonstrates what can now be achieved in evolutionary neuroscience. I do believe that they authors can be even more thorough and precise in their measurements and claims.

Reviewer #2 (Public Review):

In the manuscript entitled "Linking the evolution of two prefrontal brain regions to social and foraging challenges in primates" the authors measure the volume of the frontal pole (FP, related to metacognition) and the dorsolateral prefrontal cortex (DLPFC, related to working memory) in 16 primate species to evaluate the influence of socio-ecological factors on the size of these cortical regions. The authors select 11 socio-ecological variables and use a phylogenetic generalized least squares (PGLS) approach to evaluate the joint influence of these socio-ecological variables on the neuro-anatomical variability of FP and DLPFC across the 16 selected primate species; in this way, the authors take into account the phylogenetic relations across primate species in their attempt to discover the influence of socio-ecological variables on FP and DLPF evolution.

The authors run their studies on brains collected from 1920 to 1970 and preserved in formalin solution. Also, they obtained data from the Mussée National d´Histoire Naturelle in Paris and from the Allen Brain Institute in California. The main findings consist in showing that the volume of the FP, the DLPFC, and the Rest of the Brain (ROB) across the 16 selected primate species is related to three socio-ecological variables: body mass, daily traveled distance, and population density. The authors conclude that metacognition and working memory are critical for foraging in primates and that FP volume is more sensitive to social constraints than DLPFC volume.

The topic addressed in the present manuscript is relevant for understanding human brain evolution from the point of view of primate research, which, unfortunately, is a shrinking field in neuroscience.

We must not have been clear enough in our manuscript, because our goal is precisely not to separate humans from other primates. This is why, in contrast to other studies, we have included human and non-human primates in the same models. If our goal had been to study human evolution, we would have included fossil data (endocasts) from the human lineage.

But the experimental design has two major weak points: the absence of lissencephalic primates among the selected species and the delimitation of FP and DLPFC. Also, a general theoretical and experimental frame linking evolution (phylogeny) and development (ontogeny) is lacking.

We admit that lissencephalic species could not be included in this study because we use sulci as key landmarks. We believe that including lissencephalic primates would have introduced a bias and noise in our comparisons, as the delimitations and landmarks would have been different for gyrencephalic and lissencephalic primates. Concerning development, it is simply beyond the scope of our study.

Major comments.

1. Is the brain modular? Is there modularity in brain evolution?: The entire manuscript is organized around the idea that the brain is a mosaic of units that have separate evolutionary trajectories:

"In terms of evolution, the functional heterogeneity of distinct brain regions is captured by the notion of 'mosaic brain', where distinct brain regions could show a specific relation with various socio-ecological challenges, and therefore have relatively separate evolutionary trajectories".

This hypothesis is problematic for several reasons. One of them is that each evolutionary module of the brain mosaic should originate in embryological development from a defined progenitor (or progenitors) domain [see García-Calero and Puelles (2020)]. Also, each evolutionary module should comprise connections with other modules; in the present case, FP and DLPFC have not evolved alone but in concert with, at least, their corresponding thalamic nuclei and striatal sector. Did those nuclei and sectors also expand across the selected primate species? Can the authors relate FP and DLPFC expansion to a shared progenitor domain across the analyzed species? This would be key to proposing homology hypotheses for FP and DLPFC across the selected species. The authors use all the time the comparative approach but never explicitly their criteria for defining homology of the cerebral cortex sectors analyzed.

We do not understand what the referee is referring to with the word ‘module’, and why it relates to development. Same thing for the anatomical relation with subcortical structures. Yes, the identity of distinct functional cortical regions relies upon subcortical inputs during development, but clearly this is neither technically feasible, nor relevant here anyways.

We acknowledge, however, that our definition of functional regions was not precise enough, and we have updated the introduction to clarify that point. In short, we clearly do not want to make a strong case for the functional borders that we chose for the regions of interest here (FP and DLPFC), but rather use those regions as proxies for their corresponding functions as defined in laboratory conditions for a couple of species (rhesus macaques and humans, essentially).

Contemporary developmental biology has showed that the selection of morphological brain features happens within severe developmental constrains. Thus, the authors need a hypothesis linking the evolutionary expansion of FP and DLPFC during development. Otherwise, the claims form the mosaic brain and modularity lack fundamental support.

Once again, we do not think that our definition of modules matches what the reviewer has in mind, i.e. modules defined by populations of neurons that developed together (e.g. visual thalamic neurons innervating visual cortices, themselves innervating visual thalamic neurons). Rather, the notion of mosaic brain refers to the fact that different parts of the brain are susceptible to distinct (but not necessarily exclusive) sources of selective pressures. The extent to which these ‘developmental’ modules are related to ‘evolutionary’ modules is clearly beyond the scope of this paper.

Our goal here was to evaluate the extent to which modules that were defined based on cognitive operations identified in laboratory conditions could be related (across species) to socio-ecological factors as measured in wild animals. Again, we agree that the way these modules/ functional maps were defined in the paper were confusing, and we hope that the new version of the manuscript makes this point clearer.

Also, the authors refer most of the time to brain regions, which is confusing because they are analyzing cerebral cortex regions.

We do not understand why the term ‘brain’ is more confusing than ‘cerebral cortex’, especially for a wide audience.

1. Definition and delimitation of FP and DLPFC: The precedent questions are also related to the definition and parcellation of FP and DLPFC. How homologous cortical sectors are defined across primate species? And then, how are those sectors parcellated?

The authors delimited the FP:

"...according to different criteria: it should match the functional anatomy for known species (macaques and humans, essentially) and be reliable enough to be applied to other species using macroscopic neuroanatomical landmarks".

There is an implicit homology criterion here: two cortical regions in two primate species are homologs if these regions have similar functional anatomy based on cortico-cortical connections. Also, macroscopic neuroanatomical landmarks serve to limit the homologs across species.

This is highly problematic. First, because similar function means analogy and not necessarily homology [for further explanation see Puelles et al. (2019); García-Cabezas et al. (2022)].

We are not sure to follow the Reviewer’s point here. First, it is not clear what would be the evolutionary scenario implied by this comment (evolutionary divergence followed by reversion leading to convergence?). Second, based on the literature, both the DLPFC and the FP display strong similarities between macaques and humans, in terms of connectivity patterns (Sallet et al, 2013), in terms of lesion-induced deficit and in terms of task-related activity (Mansouri et al, 2017). These criteria are usually sufficient to call 2 regions functionally equivalent. We do not see how this explanation is "highly problematic" as it is clearly the most parsimonious based on our current knowledge.

Second, because there are several lissencephalic primate species; in these primates, like marmosets and squirrel monkeys, the whole approach of the authors could not have been implemented. Should we suppose that lissencephalic primates lack FP or DLPFC?

We understand neither the reviewer’s logic, nor the tone. We understand that the reviewer is concerned by the debate on whether some laboratory species are more relevant than others for studying the human prefrontal cortex, but this is clearly not the objective of our work. As explained in the manuscript, we identified FP and DLPFC based on functional maps in humans and laboratory monkeys (macaques), and we used specific gyri as landmarks that could be reliably used in other species. And, as rightfully pointed out by reviewer 1, this is in and off itself not so trivial. Of course, lissencephalic animals could not be studied because we could not find these landmarks, but why would it mean that they do not have a prefrontal cortex? The reviewer implies that species that we did not study do not have a prefrontal cortex, which makes little sense. Standards in the field of comparative anatomy of the PFC, especially when it implies rodents (lissencephalic also) include cytoarchitectonic and connectivity criteria, but obviously we are not in a position to address it here. We have, however, included references to the seminal work of Angela Roberts and collaborator in the discussion on marmosets prefrontal functions, to reinforce the idea that the functional organization is relatively well conserved across all primates (with or without gyri on their brain) (Dias et al, 1996; Roberts et al, 2007).

Do these primates have significantly more simplistic ways of life than gyrencephalic primates? Marmosets and squirrel monkeys have quite small brains; does it imply that they have not experience the influence of socio-ecological factors on the size of FP, DLPFC, and the rest of the brain?

Again, none of this is relevant here, because we could not draw conclusions on species that we cannot study for methodological reasons. The reviewer seems to believe that an absence of evidence is equivalent to an evidence of absence, but we do not.

The authors state that:

"the strong development of executive functions in species with larger prefrontal cortices is related to an absolute increase in number of neurons, rather than in an increase in the ration between the number of neurons in the PFC vs the rest of the brain".

How does it apply to marmosets and squirrel monkeys?

Again, we do not understand the reviewer’s point, since it is widely admitted that lissencephalic monkeys display both a prefrontal cortex and executive functions (again, see the work of Angela Roberts cited above). Our goal here was certainly not to get into the debate of what is the prefrontal cortex in a handful of laboratory species, but to evaluate the relevance of laboratory based neuro-cognitive concepts for understanding primates in general, and in their natural environment.

References:

García-Cabezas MA, Hacker JL, Zikopoulos B (2022) Homology of neocortical areas in rats and primates based on cortical type analysis: an update of the Hypothesis on the Dual Origin of the Neocortex. Brain structure & function Online ahead of print. doi:doi.org/ 10.1007/s00429-022-02548-0

García-Calero E, Puelles L (2020) Histogenetic radial models as aids to understanding complex brain structures: The amygdalar radial model as a recent example. Front Neuroanat 14:590011. doi:10.3389/fnana.2020.590011

Nieuwenhuys R, Puelles L (2016) Towards a New Neuromorphology. doi:10.1007/978-3-319-25693-1

Puelles L, Alonso A, Garcia-Calero E, Martinez-de-la-Torre M (2019) Concentric ring topology of mammalian cortical sectors and relevance for patterning studies. J Comp Neurol 527 (10):1731-1752. doi:10.1002/cne.24650

Reviewer #3 (Public Review):

This is an interesting manuscript that addresses a longstanding debate in evolutionary biology - whether social or ecological factors are primarily responsible for the evolution of the large human brain. To address this, the authors examine the relationship between the size of two prefrontal regions involved in metacognition and working memory (DLPFC and FP) and socioecological variables across 16 primate species. I recommend major revisions to this manuscript due to: 1) a lack of clarity surrounding model construction; and 2) an inappropriate treatment of the relative importance of different predictors (due to a lack of scaling/normalization of predictor variables prior to analysis). My comments are organized by section below:

We thank the reviewer for the globally positive evaluation and for the constructive remarks. Introduction:

• Well written and thorough, but the questions presented could use restructuring.

Again, we thank the reviewer, and we believe that this is coherent with some of the remarks of reviewer 1. We have extensively revised the introduction, toning down the social vs ecological brain issue to focus more on what is the objective of the work (evaluating the relevance of lab based neuro-cognitive concepts for understanding natural behavior in primates).

Methods:

• It is unclear which combinations of models were compared or why only population density and distance travelled tested appear to have been included.

The details of the model comparison analysis were presented as a table in the supplementary material (#3, details of the model comparison data), but we understand that this was not clear enough. We have provided more explanation both in the main manuscript and in the supplements. All variables were considered a priori; however, we proceeded beforehand to an exploratory analyses which led us to exclude some variables because of their lack of resolution (not enough categories for qualitative variables) or strong cross-correlations with other quantitative variables. There were much more than three variables included in the models but the combination of these 3 (body mass, daily traveled distance and population density) best predicted (had the smallest AIC) the size of the brain regions. We provide additional information about these exploratory analyses in the supplementary material, sections 2 and 3.

• Brain size (vs. body size) should be used as a predictor in the models.

We do not understand the theoretical reason for replacing body size by brain size in the models. Brain size is not a socio-ecological variable. And of course, that would be impossible for modeling brain size itself. Or is it that the reviewer suggests to use brain size as a covariate to evaluate the effects of other variables in the model over and above the effect on brain size? But what is the theoretical basis for this?

• It is not appropriate to compare the impact of different predictors using their coefficients if the variables were not scaled prior to analysis.

We thank the Reviewer for this comment; however, standardized coefficients are not unproblematic because their calculations are based on the estimated standard-deviations of the variables which are likely to be affected by sampling (in effect more than the means). We note that the methods of standardized coefficients have attracted several criticisms in the literature (see the References section in https://en.wikipedia.org/wiki/Standardized_coefficient). Nevertheless, we now provide a table with these coefficients which makes an easy comparison for the present study. We also updated tables 1, 2 and 3 to include standardized beta values.

Reviewer #1 (Recommendations For The Authors):

N/A

Reviewer #2 (Recommendations For The Authors):

Contemporary developmental biology has showed that the brain of all mammals, including primates, develops out of a bauplan (or blueprint) made of several fundamental morphological units that have invariant topological relations across species (Nieuwenhuys and Puelles 2016).

At some point in the discussion the authors acknowledge that:

"Our aim here was clearly not to provide a clear identification of anatomical boundaries across brain regions in individual species, as others have done using much finer neuroanatomical methods. Such a fine neuroanatomical characterization appears impossible to carry on for a sample size of species compatible with PGLS".

I do not think it would be impossible to carry such neuroanatomical characterization. It would take time and effort, but it is feasible. Such characterization, if performed within the framework of contemporary developmental biology, would allow for well-founded definition and delineation of cortical sectors across primate species, including lissencephalic ones, and would allow for meaningful homologies and interspecies comparisons.

We do not see how our work would benefit from developmental biology at that point, because it is concerned with evolution, and these are very distinct biological phenomena. We do not understand the reviewer’s focus on lissencephalic species, because they are not so prevalent across primates, and it is unlikely that adding a couple of lissencephalic species will change much to the conclusions.

Minor points:

• Please, format references according to the instructions of the journal.

Ok - done

• The authors could use the same color code across Figures 1, 2, and 3.

Ok – done

• The authors say that group hunting "only occurs in a few primate species", but it also occurs in wolves, whales, and other mammalian species.

We focus on primates here, these other species are irrelevant. Again, this is beside the point.

Reviewer #3 (Recommendations For The Authors):

My comments are organized by section below:

Introduction:

• Well written and thorough

• The two questions presented towards the end of the intro are not clear and do not guide the structure of the methods/results sections. I believe one it would be more appropriate to ask if: 1) the relative proportions of the FP and DLPFC (relative to ROB) are consistent across primates; and 2) if the relative size of these region is best predicted by social and/ or ecological variables. Then, the results sections could be organized according to these questions (current results section 1 = 1; current results sections 2, 3, 4 = 2.1, 2.2, 2.3)

As explained above, we agree with the reviewer that the introduction was somehow misleading and we have edited it extensively. We do not, however, agree with the reviewer regarding the relative (vs absolute) measure. We have discussed this in our response to reviewer 1 regarding the comparison of regional volumes as proxies for number of neurons. The best predictor of the computing capacity of a brain region is its number of neurons, but there is no reason to believe that this capacity should decrease if the rest of the brain increases, as implied by the relative measure that the reviewer proposes. That debate is probably critical in the field of comparative neuroanatomy, and confronting different perspectives would surely be both interesting and insightful, but we feel that it is beyond the scope of the present article.

Methods:

• While the methods are straightforward and generally well described, it is unclear which combinations of models were compared or why only population density and distance travelled tested appear to have been included (in e.g., Fig SI 3.1) even though many more variables were collected.

We agree that this was not clear enough, and we have tried to improve the description of our model comparison approach, both in the main text and in the supplementary material.

• Why was body mass rather than ROB used as a predictor in the models? The authors should instead/also include analyses using ROB (so the analysis is of FP and DLPFC size relative to brain size). Using body mass confounds the analyses since they will be impacted by differences in brain size relative body size.

Again, we have addressed this issue above. First, body size is a socio-ecological variable (if anything, it especially predicts energetic needs and energy expenditure), but ROB is clearly not. We do not see the theoretical relevance of ROB in a socio-ecological model. Second, from a neurobiological point of view, since within primates the volume of a given brain region is directly related to its number of neurons (again, see work of Herculano-Houzel), which is a good proxy for its computing capacity, we do not see the theoretical reason for considering ROB.

• It is not appropriate to compare the impact of different predictors using their coefficients if the variables were not scaled prior to analysis. The authors need to implement this in their approach to make such claims.

We thank the reviewer again for pointing that out. We have addressed this question above.

• Differences across primates in terms of frontal lobe networks throughout the brain should be acknowledged (e.g., Barrett et al. 2020, J Neurosci).

We have added that reference to the discussion, together with other references showing that the difference between human and non-human primates is significant, but essentially quantitative, rather than qualitative (the building blocks are relatively well conserved, but their relative weight differs a lot). Thank you for pointing it out.

I hope the authors find my comments helpful in revising their manuscript.

And we thank again the reviewer for the helpful and constructive comments.