The Influential Role of the Habitat on the Diversity Patterns of Free-Living Aquatic Nematode Assemblages in the Cuban Archipelago

Round 1

Reviewer 1 Report

The ms. by Armenteros et al provides an extensive analysis of nematode biodiversity in the Cuban archipelago with the aim of describing structural and functional biodiversity patterns across a wide array of habitats, including caves, coastal habitats and, even, the deep sea.

The data set is definitely impressive and the idea behind the study is worth of consideration, and would be of great interest not only for marine nematodes specialists but also for a general audience of ecologists.

I greatly appreciate the effort paid by the authors in using different functional traits of nematodes for finding out patterns of biodiversity across habitats, which is a relatively new approach. Said that, I hope and expect that this study will be made available soon to the readership of Diversity, but, unfortunately, not in its present form.

The manuscript, indeed, suffer of a series of severe biases, with potential consequences on the overall significance of the study. I guess that all issues detailed in the bullet-style list below need to be carefully addressed prior the manuscript can be eventually reconsidered for publication.

I hope that the authors will look at my suggestions constructively, as I do believe that this study could become a reference paper and would be a peaty not to see it presented in a more compelling way.

The introduction is generally clear and well written, though an overall revision of the English would make it more readable. Bibliographic references are all compellingly cited and appropriate, though some additional references (see below) would improve the significance of this study for a wider audience. Besides the environmental filter (abiotic factors), the availability of energy (food) has attracted a plethora of studies on nematodes (and many other taxa…). Some citations on this issue would be needed. What exactly do you mean with “from an anthropogenic point of view”?. Please explain or rephrase What do you mean by “habitat specificity”? Distinctiveness and beta diversity are not synonyms. Please see the point below. There are many other papers (even more appropriate) dealing with biodiversity (and beta diversity in particular) in the deep sea other than that by Danovaro et al DSRII 2013, even by the same team.. L63-64: “The ecological processes…”: this sentence is unclear and needs to be rephrased. Unless I misunderstood the sense of this sentence, I’m wondering whether, especially in an evolutionary context, it could not be considered the opposite: Are patterns in the field the most important factors explaining traits? There are a few very recent papers on nematodes assemblages in tropical areas by Semprucci and collaborators. These could be of interest for the authors and some of them could be included. The concept of beta diversity is much wider than simply representing a way to identify patterns across scales (differentiation diversity). Besides the debate on the actual significance of Bray-Curtis similarity as a beta diversity index, a non-secondary approach for measuring beta diversity is to consider its two components: wherever communities are not identical beta diversity should be described with turnover and nestedness, since the only processes needed to generate all the possible patterns are species replacement and species loss (or gain). Bray-Curtis similarity (or dissimilarity) provides just a surrogate analysis of habitat similarity, but it has a very low power for identifying patterns (and explanatory factors) of community change (beta diversity). For this reason, I would invite the authors to use other descriptors of beta diversity and, in particular, to reconsider their logical framework measuring the two components claimed above. For a methodological reference, please consider the paper by Andrés Baselga (Partitioning the turnover and nestedness components of beta diversity, Global Ecology and Biogeography 2009). Prior to do this, the authors should also consider my comment below dealing with the taxonomic level of the data set used in this study for measuring species richness. The sampling effort is huge, but the strategy is under explained: I would assume that habitats available along the Cuban archipelago are more than those considered in this study. What is the rationale for this “selection” of habitats? I do not think you can assign each macroalga to a single habitat. Could you please explain this choice and support it with relevant references? Sampling method adopted in each habitat should be reported (with details) at least in the supplementary material. How biodiversity estimates from different substrates were standardized? How can you compare a number of species in 1 cm3 of muddy sediment with a number of species from macroalgal talli? How samples from hard and soft substrates were normalized for standardization? This information is crucial for interpreting the study. As far as the sampling in the deep sea is concerned, I’m wondering whether the three replicates collected in each of the 9 sites were obtained from independent deployments of the corer or not. This would make a huge difference in interpreting the number of species retrieved… The sieves used are not the right ones. Currently, for nematodes biodiversity a sieve of 30 microns (even 20 for deep sea assemblages) are preferred. While for coastal habitats the choice can be tolerated, the data from the deep-sea sites could be severely biased (underestimation of species number). I see this could not be solved, but it should be recognised, especially in the discussion. I see that the authors identified nematodes at “the lowest taxonomic level”, but it is unclear then how they measured species richness: did they use the number of the lowest recognised taxa, only genera (in this case they should refer to genus richness…), only species? The authors should specify better at which level they measured species richness. If mixed taxonomic levels were considered, then the robustness of the results and the discussion would be very limited. I’m not convinced of eliminating singletons: there are evidences that some “rare” species/taxa col be the key for interpreting patterns across scales (I would expect this could be relevant when comparing assemblages from different macroalgae) In a paper addressing beta diversity across habitats, it would be interesting getting information on which species/taxa (or groups of species/taxa) are responsible for differences across habitats (SIMPER tests): this is relevant especially whether beta diversity patterns are differentially explained by species/taxa turnover vs. loss (gain). Another missing point is that the authors did not consider potential covariates, one of which, potentially relevant, is water depth (a sort of surrogate for marine sites - not caves – of food availability). While the data apparently conciliates with the DEM, the authors should also refer to the IDH, foreseeing highest biodiversity levels at intermediate levels of disturbance, as either physical disturbance and resource availability are “limiting factors”. The importance of resource availability is claimed in the last part of the discussion, but the observed patterns are discussed without having any actual measurement of resources. This limits this part of the discussion to an inferential (weak, though reasonable) interpretation.

Author Response

Please see the attachment

Author Response File: Author Response.docx

Reviewer 2 Report

Review of Diversity 2019, 11,

This is a very good paper on an understudied region that looks at the diversity of nematodes from different habits. The research covers 60 sites in nine different habitats.  The sampling techniques have been well coordinated to allow comparison of the habitats. The data analysis is thorough and presented well in figures and tables. The biological traits analysis in relation to the habitat they occur in is detailed and the authors have conducted a good review of the literature in the discussion.

Most of the minor grammatical edits have been pointed out in the attached pdf file.

Some additional comments:

Although this paper compares and summarizes data from earlier studies (given in supplementary table 1), it may help to give a little more information particularly in the discussion of results to explain some of the differences/variations noticed between and among the sites.

In the site descriptions, it may worth noting the following points as they may affect the distribution patterns that are discussed later.

-Do freshwater caves have any source of water from land such as runoff above ground.

-Are some of the coastal sites such as bare sand, unvegetated mud, subject to tidal fluctuations.

Line 211. Check the spelling of ‘punctuated’ in the nematode literature as the correct description of the cuticle ‘pores’ is punctated or punctations. Also, check this spelling in the supplementary table 2.

Line 360. If many species with one or two individuals are removed, could it affect data.

Line 434. Could isolation of these habitats be contributing to unique assemblages in caves. 

Line 437 and elsewhere: there is mention of ‘similarity in the assemblage structure’ but no reference to another publication where this may be published. If this data is not published elsewhere, it would be helpful to have supplementary data tables for this information.

Lines 445-446. Could the ‘passive dispersal’ be facilitated by local bottom currents

Comments for author File: Comments.pdf

Author Response

Please see the attachment

Author Response File: Author Response.docx

Round 2

Reviewer 1 Report

I read with much interest the revised version of this manuscript and the attached rebuttal letter. Overall, I found the responses of the authors to almost all of my questions/criticism compelling and well argued. However, there are a few points, that, in my opinion, would require some minor amendments to match the last version of the manuscript with the argumentations given by the authors in their rebuttal letter.

To facilitate the authors’ and the editor’s check, I’ve provided below a point-by-point reply to the authors’ letter.

English usage was revised and improved, reviewer 2 made many edits on the pdf version and we made most of the suggested corrections.

R: Ok, much improved indeed.

We have detected only one reference (Baselga et al. 2009) suggested by the reviewer. However, as we are not convinced to apply the Baselga’s approach (see below), we did not add this reference.

R: Ok, see also below.

We have included in the introduction (L68-73) the reference to the Dynamic Equilibrium Model (DEM), as well references to other two relevant and previously proposed hypotheses (Intermediate Disturbance and Species-Energy). However, these hypotheses refer more to diversity itself than to habitats, so, we put in the 3^rdparagraph and not in the first paragraph (that refers to habitat types).

R: Ok, well done.

We have changed “anthropogenic point of view” × “operational point of view”, and added an example of the meaning in the text.

R: Ok.

We have removed this sentence since “habitat specificity” term is peripheral to the objective of our study and it was unclear within the context.

R: Ok.

Distinctiveness and beta diversity are not synonyms. Please see the point below.

R/ Partially agree. This statement is debatable, we have traced back the term distinctiveness to the seminal work by Colwell & Coddington (1994). Latter authors used “distinctiveness in species composition” as definition of complementarity which includes β-diversity, distance, and dissimilarity (p. 103). However, for the clarity’s sake, we removed all references to distinctiveness and used only β-diversity with the corresponding definition following Anderson et al. (2011) (L54-55).

R: Although I and – I’m sure - the authors themselves could discuss a lot on this point, I support the choice of eliminating any reference to distinctiveness.

The selection of a single appropriate reference (as example) for such general statement (i.e. “ecological processes driving the β-diversity … in the deep-sea”) is subjective. We have 50 articles focusing on nematodes & diversity & deep-sea, and very few of them have the quality of Danovaro et al. (2013). They directly measured several drivers of assemblages (prokaryotic abundance, phytopigments, biopolymeric C) at several spatial scales and at species level. They also used functional traits and worked, at least in one station, to similar depth of our samples. However, if the reviewer mentions the details of any other relevant paper, we would include it.

R: Drivers of beta diversity in the deep sea are considered also in the following papers (maybe with different methods and indexes –especially for beta diversity – but, in my opinion they are all relevant for the topic covered by your manuscript, and at least some deserve to be cited:

Danovaro et al Global Ecology and Biodiversity (2014)

Bianchelli et al Biogeosciences (2013)

Danovaro et al MEPS (2010)

Pusceddu et al DSRII (2009)

Leduc D et al 2012 MEPS

Zeppilli et al 2016 Scientific Reports

We have rephrased the sentence (L60-62).

R: Ok, well done

Unless I misunderstood the sense of this sentence, I’m wondering whether, especially in an evolutionary context, it could not be considered the opposite: Are patterns in the field the most important factors explaining traits?

R/ We disagree and did not modify the idea, which was originally stated by McGill et al. (McGill, B.J.; Enquist, B.J.; Weiher, E.; Westoby, M. Rebuilding community ecology from functional traits. Trends Ecol. Evol. 2006, 21, 178–185). The point is rather about philosophy, and maybe we do not understand the remark. However, patterns are regularities in some quantity (e.g. trait abundance, richness) that we can measure and it is supposed they are as much objective as possible. Explanations are matter of ideas, as they may change depending of the observer.

Indeed, I must admit that my comment was a little cryptic and I apologize for this. My intention was not questioning the validity of McGill’s and the authors’ approach. I was just wondering whether the community structure (determined by environmental variables) could shape, in evolutionary terms, the nematodes traits, instead of hypothesizing that traits determine community structure, thus basically whether inverting the causal relationship between community structure and traits could make sense. I admit that this is a (subjective) question and, moreover, the eventual answer is out of the scope of the manuscript. I thus definitely accept the authors’ position,

We have included two papers by Semprucci et al. (2014; 2018) and two by Raes et al. (2007; 2008).

Ok, well done

We are aware of the approach proposed by Baselga et al. (2010) for the partition of theβ-diversity in turnover and nestedness. Also we have analyzed the debates about the subject: 1) Multiplicative vs. additive partition of β-diversity [Jost (Ecology 2007, 88, 2427-2439) vs. Baselga (Ecology2010, 91, 1974-1981)]; and 2) Methods for partition in turnover and nestedness [Baselga (Global Ecol. Biogeogr., 2010, 19, 134-143; Baselga & Leprieur (Methods Ecol. Evol., 2015, 6, 1069-1079) vs. Podani & Schmera (Oikos, 2011, 120, 1625-1638)]. We consider that the use of multivariate measures of β-diversity (e.g. Bray-Curtis index) is superior to the use of α- and γ-components (whatever multiplicative or additive approach used). Multivariate approach to measure β-diversity is conceptually simple, strongly entrenched (and accepted) in the ecological literature and it is connected with a set of non-parametric techniques for visualize results (MDS), test for patterns in central position (PERMANOVA) and dispersion (PERMDIST), and highlight the species which more contribute to the patterns (SIMPER). The multivariate approach has been nicely summarized by Anderson et al. (Ecol. Letters, 2011, 14, 19-28). We have used all the mentioned multivariate techniques in our contribution to complete to objectives, and we believe that add another sophisticate approach will bring an additional layer of non-needed complexity.

R: I can understand the point raised by the authors and can agree that adopting the Baselga’s approach would require a thorough revision of the working approach. In principle, I can agree also with the authors that the Bray Curtis index is simple and the associated tests used to investigate patterns of beta diversity are the most utilized in the literature. I, instead, do not agree that this is the most comprehensive way to investigate and describe beta diversity (patterns). However, as this, once the manuscript will be published, could become a point of larger debate among the Diversity readership (and more), I would invite the Editor to consider valid the point raised by the authors, leaving the scientific community to discuss on it. At the same time, for clarity, I would appreciate whether the defense the authors made of their approach in the rebuttal letter would be clearly stated in the manuscript (recognising that other metrics and approaches can be used for measuring beta diversity and investigating its spatial variability).

We added a sentence in M&M (L118-120) saying that habitats were selected based on perceived importance in terms of diversity for Caribbean aquatic ecosystems and that some other habitats could not be included (e.g. mangroves, beaches).

R: Ok, well done

Previous published work (Pérez-García et al. 2015, J. Mar. Biol. Oceanogr., 4, 7) concluded that the macroalgae species (six species with different degree of complexity were tested) did not influenced the SR neither species composition, although epiphytic assemblages differed from surrounding hard substrates. In addition, we have formed a group of sites containing epiphytic nematodes, which is radically different to the other considered assemblages that are infaunal (e.g. seagrass beds) or epilithic (e.g. coral degradation zones). We have added more information and relevant reference to the description of each habitat type in M&M and also in the discussion a line about the lack of differences among macroalgae species with the appropriate reference (L471-474).    

R: The additional information helps to sustain the authors’ contentions, but I’m not fully convinced, yet. My perplexity remains as for defining a single species as a habitat. Again, this could be a matter of terminology and the scientific community will eventually debate on this.

We have added a column in the supplementary table S1 with details about sampling and processing methods (e.g. mesh size).

R: Ok, well done

Data were not standardized at all; that is, we have worked with number of individuals and number of species. There is not a feasible way to standardize data coming from so disparate habitats such as a macroalgae thallus, coral rubble, and bare sediment. However, we can compare numbers from these habitats, the point is to keep in mind for the discussion/explanation the bias of each method and how they can influence the results. We have added a paragraph (L395-400) with words of caution in the interpretation of absolute values of abundance in our work.

R: Ok, much appreciated

We added the information about the sampling details in deep waters (and also for the other habitats) in a new column of supplementary data S1 and in M&M (L190).

Ok, well done

Indeed, we collected the three replicates from the same deployment of multicorer.

As I suspected, this is a weakness, though with no solutions. The authors should clarify this and recognize the potential biases (see also below).

We consider this is the most effective sampling strategy to capture the diversity metrics (SR and β-diversity). Montagna et al. have compared sampling methods for deep-sea infauna in deep-sea of Gulf of Mexico (Limnol. Oceanogr.: Methods, 2017, 15, 166-183). They demonstrated that most of the variance in both SR and abundance of macrofauna was associated to differences between sites (65%), differences between pseudoreplicates (i.e. between cores in a single deployment) (28%), and after between true replicates (i.e. deployments) (9%). Since meiofauna distribution varies at even smaller scale than macrofauna, this result about scales of variation should hold also for nematodes. Therefore, with our sampling design we were able to capture most of the variability associates to the diversity; that is the ones that occur between sites and between cores in a single deployment.

R: Again, I’m not convinced. The work by Montagna et al. did not consider Nematode species richness and as far as I can see did not consider the effect of pseudoreplication on meiofauna, but only on macrofauna (as correctly stated by the authors in their rebuttal letter). Again, since it is impossible for the authors repeating the study, I would just see this issue recognized as a potential bias on the manuscript, or, at least, providing support to their approach including in the manuscript the defense reported in their rebuttal letter.

The sieves used are not the right ones. Currently, for nematodes biodiversity a sieve of 30 microns (even 20 for deep sea assemblages) are preferred. While for coastal habitats the choice can be tolerated, the data from the deep-sea sites could be severely biased (underestimation of species number). I see this could not be solved, but it should be recognised, especially in the discussion.

R/ Partially agree. We added in table S1 the size of mesh used for each habitat type. We added a couple of sentences in the discussion (L377-380) about the potential bias of small-sized species in deep water habitat. However, we have data about morphometry (Armenteros et al. Body size distribution of free-living marine nematodes from a Caribbean coral reef. Nematology2015, 17, 1153-1164) in four coastal waters using 45 µm sieving. Median body width was 43 µm (interquartile range: 32–59 µm) suggesting that this mesh size may capture small-sized nematodes reasonably well.

R: Not agree. “Reasonaby well” is not necessarily scientifically robust. Any deep-sea nematologist would question this choice. The authors have, however, defended their approach in the amended manuscript and this, for me, is the minimum. This point, as others above, will be eventually a matter of debate by the scientific community,

We clarified better in M&M the used taxonomic level that was species level (L194-198).

R: Ok

The primary criterion to include species in the analyses was that they were reasonably well identified. In other words, we “cleaned” the database for taxonomic accuracy, not because the rarity itself. We removed several potential species because we had only a one individual (mostly juvenile or female) that could not be assigned with confidence to any species. The basic assumption underlying is that it is an error to included misidentified species in the matrix. This is because we removed this paragraph from the manuscript. We rephrased a part in the discussion related with the bias in the identification (L362-365)

Ok, well done

We believe that the best way to represent the species responsible for differences across habitats is the list in the table 1 which show a different set of “typical” species for each habitat. Formal pairwise comparisons of dissimilarity among the nine habitats would yield an unmanageable number of comparisons (i.e. 36). We were able in the text, in a qualitative way, to highlight those species responsible of patterns that were represented in the table 1.

R: I still remain doubtful as I still miss which is the criterion used for defining “typical” species.The authors must find the way to provide at least a semi-quantitative estimate.

We added a couple of sentences in the discussion about the limitation due to the lack of abiotic measures that may reveal drivers (e.g. polymeric C, grain size) (L388-390). However, in coastal areas, in the small depth range that we have worked out (about 2–20 m), depth is not a clear surrogate of productivity since hydrodynamic regime, type of primary producers (e.g. seagrasses, microalgae) and local source of nutrients are more important for food availability. Therefore, it is meaningless to correlate depth with diversity metrics; we explained this in the discussion (L390-394).

R: Ok.

We have introduced the IDH in the introduction section as a context of the DEM; namely, we added that latter theory adds another layer of complexity (i.e. resource availability) to disturbance (proposed in the IDH) (L70-73). As indicated in the previous point, we have added a couple of sentences in the discussion about the lack of measurements and the weakness it brings to the explanations.

R: Ok.

Author Response

Authors: We thank very much to the reviewer 1 for the comments and ideas given to us to improve the manuscript. Here we address some of the comments that need a further action from us (i.e. those that do not say ok). We appended a version 3 of the manuscript with track changes mode; and the same "clean" version 3.

Reviewer 1. Drivers of beta diversity in the deep sea are considered also in the following papers (maybe with different methods and indexes –especially for beta diversity – but, in my opinion they are all relevant for the topic covered by your manuscript, and at least some deserve to be cited: Danovaro et al Global Ecology and Biodiversity (2014); Bianchelli et al Biogeosciences (2013); Danovaro et al MEPS (2010); Pusceddu et al DSRII (2009); Leduc D et al 2012 MEPS; Zeppilli et al 2016 Scientific Reports.

Authors: Agree. We added a reference (Rosli et al. 2018) in the previous version. Now, we further add one more from the suggested pool: Pusceddu et al. 2009.

Reviewer: I can understand the point raised by the authors and can agree that adopting the Baselga’s approach would require a thorough revision of the working approach. In principle, I can agree also with the authors that the Bray Curtis index is simple and the associated tests used to investigate patterns of beta diversity are the most utilized in the literature. I, instead, do not agree that this is the most comprehensive way to investigate and describe beta diversity (patterns). However, as this, once the manuscript will be published, could become a point of larger debate among the Diversity readership (and more), I would invite the Editor to consider valid the point raised by the authors, leaving the scientific community to discuss on it. At the same time, for clarity, I would appreciate whether the defense the authors made of their approach in the rebuttal letter would be clearly stated in the manuscript (recognising that other metrics and approaches can be used for measuring beta diversity and investigating its spatial variability).

Authors. We agree. We have added the following sentence in the introduction: "The partition of the β-diversity in α- and γ-components, using additive or multiplicative relationship, is a feasible approach to disentangling the effects of scale or other nested units of analysis". Also, we added the word "alternative" referring to B-C approach.

Reviewer. Again, I’m not convinced. The work by Montagna et al. did not consider Nematode species richness and as far as I can see did not consider the effect of pseudoreplication on meiofauna, but only on macrofauna (as correctly stated by the authors in their rebuttal letter). Again, since it is impossible for the authors repeating the study, I would just see this issue recognized as a potential bias on the manuscript, or, at least, providing support to their approach including in the manuscript the defense reported in their rebuttal letter.

Authors: We added the following sentences in the M&M section: "The three cores collected from a single deployment were in rigor pseudoreplicates; but, the bias on the diversity estimates should be small, if any. This is because: (i) we combined the three cores to obtain a more robust estimate, and (ii) meiofauna (and nematodes) vary at spatial scales smaller than 1 m, therefore the three cores (separate ~ 1 m) could effectively sample the variability in the distribution (and hence the diversity).

Reviewer: I still remain doubtful as I still miss which is the criterion used for defining “typical” species.The authors must find the way to provide at least a semi-quantitative estimate.

Authors: Agree. We have added in M&M section the following sentences to explain the rationale to use SIMPER for highlighting species: "We applied the SIMPER procedure in order to identify the species responsible of the compositional differences among habitats using the PRIMER 6.1.15. Formal pairwise comparisons among the nine habitats yield 36 lists of species (i.e. habitat 1 versus 2, 1 versus 3, etc.) contributing to the pairwise dissimilarity, which is an unmanageable number of lists. Therefore, we presented those species that contribute up to 50% of cumulative similarity within habitats. We considered that the selected species were typical of a particular habitat type since they occurred at most (or all) of their sites. The comparison in a table of the presence/absence of species indicates those species that most contribute to the β-diversity patterns across the nine habitats.

Reviewer 2 Report

The authors have made significant changes to the manuscript and it has improved considerably. The paper will be a valuable contribution to the knowledge of biodiversity and ecology of an abundant yet understudied taxon. Please check the supplementary table of biological traits on the spelling of 'punctuated' that should be 'punctated'.

Author Response

Thank you very much to the reviewer 2.

We have checked again the supplementary table 2. Only the correct word "punctated" is there.