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I am happy to accept your manuscript. We can incorporate the very minor comments of reviewer 3 at the proof stage. Congratulations!
[# PeerJ Staff Note - this decision was reviewed and approved by Patricia Gandini, a PeerJ Section Editor covering this Section #]
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The authors addressed all of the reviewers' comments, including those regarding the analyses and parameters used, and the manuscript has improved substantially. The manuscript is easy to read and draws interesting conclusions, especially regarding the conservation of gallery forests/savannas. I found only one minor sentence that needs to be fixed in Lines 383-384 where it reads "Indicators of landscape structure explained more the variation of the three biodiversity dimensions that indicators of vegetation structure." which could be fixed as "Indicators of landscape structure explained more of the variation in the three biodiversity dimensions than indicators of vegetation structure."
Good luck on your future research, sincerely,
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I am generally happy with the efforts by the authors to attend to my comments and those of the other reviewers which have resulted in a strengthened manuscript.
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The manuscript has greatly improved with the authors' review. I only have two small changes:
L 163: replace "(4)" with "(3)"
L 478: replace "Maria Alice Alves" with "Maria Alice S. Alves"
The three reviews are very thorough and two of them suggest important issues around the trait categorization, especially for dispersal ability. You will have to think carefully about how the point count data was originally collected (reviewer 2) and some reanalysis will be required.
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The manuscript is very interesting, with clearly stated objectives and conclusions. It represents a good addition to the literature regarding gallery forests and savanna ecosystems. Below I present suggestions on specific parts of the manuscript. Of major concern are some aspects of the methods that need clarification and/or reevaluation. Specifically, I do not consider the proxy for dispersal ability a good choice as the measure could be correlated to several other species-specific traits and I suggest its removal from the analysis. I hope the authors will find my comments useful to improve their manuscript.
Abstract:
(1) change “porcentage” to “percentage”
Introduction:
Line 56: remove ‘s’ from “savannas”
Line 68: remove ‘s’ from “centers”
Lines 69-74: “Regions” are repeated a lot in these phrases, and it could be reworked to read better. I suggest briefly stating that gallery forests are part of savanna ecosystems (i.e. of the savanna regions) as it would possibly make it easier to rework the statements.
Lines 87-91: It is important to note that, as mentioned by the authors, Forman (1995) also considers other functional traits – not only dispersal ability – by mentioning that generalists would dominate the GF communities. Therefore, it is important to mention “generalism” in addition to dispersal ability. Also, I think that it would interesting if the authors present about the expected drivers of the differences in community composition and its expected nestedness, more specifically regarding the habitat attributes (e.g. proximity to adjacent forest?).
Methods:
Line 175: add ‘,’ between “lianas” and “dead trees”
Lines 188-191: In every transect (site) there were 21 measurements of litter depth (3 plots x 7 measurements/plot). Please, double check the total of 63 measurements per transect (site).
Line 198: change “was” to “were”
Line 203-204: Was the sampling order of point counts randomly assigned such that the time of sampling would not interfere in the results (e.g. one site is always sampled at 6am and has higher species richness than a site that has always been sampled at 10am due to reduced species activity)?
Line 216: Please, cite the literature from where the body mass data was obtained.
Lines 218-221: I consider that it is not a good measure of species dispersal ability as many other specific traits might influence how far a species can move into the savanna. For example, in the dataset there are species that are well adapted to open vegetation areas with scattered trees, like Elaenia flavogaster, Myiarchus ferox, Thraupis spp., among others, for which this proxy for dispersal ability would not make sense. Therefore, I suggest removing it from the analyses (even though a correlation was found between this variable and abundance and occupancy) or removing species characteristic of open vegetation and reanalyzing a subset of the data composed only of forest-dwelling species. Also, I could not find Sousa’s dissertation to evaluate their methods, not even at Universidade Federal do Amapa’s online library system. On the other hand, the authors already have a proxy for dispersal ability, the HWI data taken from Sheard et al. (2020). Yet, it also is important to note that, although Sheard et al. (2020) calls it HWI, they actually measured the Kipp’s Index (1959), not the HWI as presented by Claramunt & Wright (2017) and Claramunt et al. (2012). Claramunt & Wright’s HWI has a standardization for body size (wing length) in their formula, not used by Sheard et al. (2020).
Line 230: Please, add the conditions that determined if a species well-sampled.
Lines 237-239: Please, cite a reference for this standardization. If it was not taken from the literature, but is a common practice, it should be explained further.
Line 252: Should it be VIF < 3? If not, how much higher than 3? If VIFs are too high, one or some of the variables should be removed from the analyses.
PGLS, AICc, and model selection: (1) To compute the model average presented in Tables 1 and 2, were only the models with delta < 2 used? If not, would you consider using only those models with delta < 2, as those are considered the most informative?
(2) In the PGLS analyses, categorical variables should be added to the models by dummy coding them (Mundry, 2014), but it seems that was not the case for foraging stratum groups. I suggest performing the analyses again and using dummy coded variables for foraging stratum.
Mundry R. (2014). Statistical issues and assumptions of phylogenetic generalized least squares. In
Modern phylogenetic comparative methods and their application in evolutionary biology (ed. LZ Garamszegi), pp. 131–153. Berlin: Springer.
Results:
Line 338: italicize Dendrocolaptes certhia
Line 354: The sample size is small (26) and the number of models tested is too high, reducing the power of the AIC to detect the best model (check Burnham & Anderson [2002] book and their discussion about it – number of models x number of variables x sample size). I believe this issue is reflected in the low values of the AIC weights for the models (or, alternatively, all models are performing poorly in describing the data). Therefore, I would suggest that the authors select a smaller set of biologically meaningful models for testing, instead of using all the possible model combinations as it has been done. In the way the analysis was performed it is impossible to tell models apart and determine which factors are correlated with taxonomic, functional, and phylogenetic diversity in the study system.
Discussion:
Lines 384-386: I still am unconvinced that the distance is correlated with, or a proxy for dispersal ability. I think other functional traits might be affecting how far a species move into the open savanna, i.e. habitat preferences, diet, or foraging behavior. In other words, the traits that would make the species tolerance to the savanna ecosystem higher (a generalist), but not necessarily dispersal capability.
Line 409: Add a period (.) after “(Mustin et al., 2017)”
Line 417: change “gallery forest” to “birds”
Conclusion:
Lines 453-454: the correlation between PD and understory foliage density is not presented in the discussion. Please, add a discussion about the processes that might be driving it and its significance in the study.
Figures and tables:
Figure 1: in the box within the map, change anthropism for anthropogenic, disturbed, or similar word.
Tables 1 and 2: these tables results from similar analyses, thus I suggest standardizing their format.
Generally clearly written and well constructed, historical literature appropriately treated and figures OK - note Fig 1 will be inaccessible for R-G colourblind readers.
MS within the scope of the journal and fairly novel. It would have been useful to understand whether the community composition is a nested subset of surrounding terra firme forests, or a novel community of fragmentation tolerant and edge species. Looking at the list more species seem to be the latter - the two most abundant species are Tolmomyias flaviventris and Turdus leucomelas which are not associated with undisturbed forest habitat in Amazonia and Formicivora grisea is a not a forest-associated species at all. The sample size is rather small and the sample contains a long tail of rare species, several of which I wouldn't expect to be rare, so good to emphasize the knowledge of the surveyor.
A lot of the paper hangs on the 'species' dispersal ability' scores taken from an unpublished MSc thesis. A much better rationale needs to be made for using these scores which are opaque. Several of the species e.g. Formicivora breed in the savannas so I don't see how this is measuring dispersal and not just tolerance of non-forest habitats. It seems odd to have Querula have a 'dispersal score' of 0 when it is a large bodied bird which is a very strong flyer with a mid-range HWI. The HWI is itself a measure of dispersal capacity. I would seek to categorise species by habitat preference using an external dataset.
I did wonder about using unlimited radius point counts with only 200m between points - some Amazonian species can easily be detected at 200m risking double-counting and hence pseudoreplication when summing data across points.
The landscape scale habitat coverage section is poorly treated, many of the corridors are situated a long way from forest nodes, it might be useful to capture both this variation and habitat availability at wider buffer widths - also corridor width seems important and in combination may explain the presence/absence of forest-associated suboscines. I have generally found that investing lots of effort in local habitat variables explains little as they vary so much in space and birds often have large territories, the authors should seek to glean more information about habitat at landscape scales.
The section on general traits of species in the study area e.g. L342 seems out of place when the authors have had to constrain their community due to sampling issues - bigger species will have been excluded for example.
The lack of predictive power of the env variables could be improved by considering more landscape variables describing habitat amount, habitat quality and connectivity.
I struggle with the 'selective colonization' paradigm - how is this different from habitat filtering?
Abstract 'porcentage' = 'percentage', nestedness pattern = nested pattern
L52 are Neotropical savannas 'regions' or 'habitats'
L53 also silvioculture - e.g. in AP eucalyptus and in PA oil palm
L60 do gallery forests sustain savanna species? Is Burhinus in the galley forest?
L79 surely gallery forests are also totally structurally distinct from terra firme forest - hence habitat filtering.
L112 the MAPITIOBA frontier also vies for this title.
L200 4 visits isn't enough to capture most species - the regional species pool includes lots of species that were not recorded.
The manuscript is well structured and clearly written. Sufficient field background/theoretical context is provided. The structure in terms of tables, figures and raw data is apropriated. The questions are clear and the authors found relevant results to them.
The study is original and in the scope of the journal. The research questions are clear, relevant and meaningful. It is stated how the study fills an identified knowledge gap. The investigation was performed to a high technical standard. The methods are described in detail and can be replicable.
In Methods, in the sub-item "Species functional traits" the authors mentioned that the body mass for all species was gathered from the literature, but did not include the references used for that, which need be added. In the sub-item "Species Selection" it will be good to include what is the minimum amount used to consider a species as "well sampled".
The underlying data have been provided and they are robust and statistically sound. The discussion is appropriated, the conclusions were well stated and linked to the research questions. The second part of the conclusion (Lines 460 to 481) seems more appropriated to be included at the end of the discussion instead as in "conclusion."
The manuscript approaches a relevant issue for biodiversity conservation. The authors proposed strategies on how gallery forests can be managed to maintain bird species assemblages in face of the fast anthropogenic activity in the tropical landscape. A result to be highlighted as a new finding is that increased human activities in the landscape was negatively correlated with taxonomic and functional diversity of gallery forests. This supports the idea that in tropical landscapes, extrinsic factors (e.g. matrix dynamics), are as important as intrinsic factors to explain the ecological processes occurring within habitat patches. Based on their results, the authors indicated recommendations for conservation of gallery forests, which are important to the maintenance of a substantial part of the biodiversity in neotropical savannas.
Specific suggestions/comments were included in the PDF file of the manuscript.
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