Four in One: Cryptic Diversity in Geoffroy’s Side-Necked Turtle Phrynops geoffroanus (Schweigger 1812) (Testudines: Pleurodira: Chelidae) in Brazil

Round 1

Reviewer 1 Report

Dear editor and authors,

In my opinion this is an interesting paper to be published in this Journal, and I only propose some suggestions:

- “cryptic diversity” is included both in the title and in the keywords: it is recommended that the keywords are always different from those used in the title

- Line 97: It may also be interesting to indicate that some morphological characters have also been considered, such as the coloration and the patterns of marks on the head and the plastron.

- Lines 416-417: “However, there are differences in non-morphometric characters including color of the carapace, plastron and lateral bands and stripes on the head”/Lines 436-437: “there are difference in (…) color pattern of individuals from these two river basin.” I suggest developing these interesting ideas, not only indicating that there are differences (which are not explained), but describing them. In fact, the abstract indicates “but are characterized by differences in coloration and patterns of marks on head and plastron” so its development in this paper is expected.

- Lines 42-422: “Phrynops geoffroanus is also replete with junior synonyms that although currently considered invalid may, in fact, be valid taxa”. Why not develop this section further, indicating to which specific name each of the species/lineages identified here could correspond?

- It would be advisable to add a brief “Conclusions” section, compiling the main ideas provided in this paper (or, if this is not possible, change the title of the “Discussion” section to “Discussion and Conclusions”).

I’m available for any questions that may arise.

Sincerely,

Author Response

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Author Response File: Author Response.pdf

Reviewer 2 Report

I congratulate the authors of "Four in one: Cryptic diversity in Geoffroy's side-necked turtle Phrynops geoffroanus (Schweigger 1812) (Testudines: Pleurodira: Chelidae) in Brazil" on their excellent work and presentation. The methods are appropriate and the findings are well-supported. Aside from some minor suggestions below, I support Acceptance of the manuscript. 

• Ln 103-109: Over what time span were your sampling efforts?
• Ln 148: Missing GenBack accession numbers
• Ln 249: misspelled "components" in the second usage
• Table 1 appears to be cut off on the right side
• Table 2: Reduce the number of decimal places used
• Fig 3 & 4: the resolution makes these figures hard to read
• Ln 298: "1.2" repeated when describing age range
• Ln 35 and 331: change "habitat" to "biome" to stay consistent with the rest of the manuscript
• Ln 356-357 and 372-373: Since basin and biome are highly correlated, can you differentiate the affects on speciation?
• Ln 360: add a colon after "species complex" instead of a period
• Ln 374: "... there were no statistically ..."
• Ln 392: "... while in the four species ..."
• Ln 404: "similarly"
• Ln 427-451: If the species cannot be readily differentiated in the field, can you discuss options for conservation that don't rely on individual identification (e.g., conservation at the basin-scale, as distinct population segments or management unit, etc.)
• Minor grammatical changes throughout the manuscript including use of the Oxford comma to differentiate the penultimate and final items in a list within a sentence and isolating examples within parentheses (e.g., ...)
• Font changes in Ln 119, 146, and 254-255. Not sure if this is on the original manuscript or an artifact of my PDF download.

Author Response

Please see the attachment

Author Response File: Author Response.pdf

This manuscript is a resubmission of an earlier submission. The following is a list of the peer review reports and author responses from that submission.

Round 1

Reviewer 1 Report

This study combines mtDNA, ddRADseq, and morphometric data to elucidate species limits in Phrynops geoffroanus throughout South America. The authors use the mtDNA to create gene trees, which are used as input for several single locus species delimitation methods. The genomic data are also used to estimate a genealogy in BEAST. Finally, the authors collect and analyze several morphometric characters for both males and females. The results support four main mtDNA lineages of moderate divergence. Species delimitation results are fairly congruent, with most supporting four 'species'. The morphometric data showed limited utility in discriminating individuals based on their genetic lineage, though there was some morphological divergence in Lineage 4. Finally, the authors provide evidence for some color pattern and shape variation that may be useful to diagnose species.

The quantity and types of data collected in this study were sound, and the questions raised were important. However, I have several major concerns that will need to be addressed. My biggest concern is that the conclusions of the study are not supported by the analyses performed. Although the authors collected genomic (ddRAD data), analyses with these data were very limited and unclear. Instead, it appears that the authors chose to rely primarily on the mtDNA results. The limitations of mtDNA are well-known, but the authors do not address these in the manuscript. It seems like the authors simply take the results of their single locus species delimitation analyses at face value. Most systematists would not rely exclusively on these data and results to delimit species. Instead, they can be used to help form initial hypotheses that can be tested with additional data and analyses. Unfortunately, this was not done in this paper. No validation-based species delimitation analyses were performed with the genomic data. Why? You have the data, so why not use them?

Analyses of the genomic data were extremely limited and unclear. The authors state that they performed a species tree analysis, but I am not sure this is correct based on what is in the Methods. Concatenating genomic data and running BEAST is not really a species tree analysis. Was starBEAST used? If so, how were individuals assigned to putative species? What priors and parameter settings were used? The authors have spent time and money collecting these data, so why not spend more time analyzing them more thoroughly?

There are many minor spelling and grammar mistakes (and typos) that I will not list. The authors should carefully re-read their paper to address these. Also, why are there multiple font sizes?

I would try to avoid overly confident conclusions that the four mtDNA lineages are different species. Again, this comes back to the limitations of mtDNA data. You have evidence for four mtDNA lineages that may or may not represent distinct species. The current set of analyses does not allow us to make this distinction with any confidence.

As the authors make reference to different river drainages, it might be useful to add these to the map.

Line 134: What was the denaturation temperature for 16S?

Line 166: Requiring data present in at least 75% of individuals is likely too conservative, and you risk throwing out useful data. Why was this value chosen? I was quite surprised that only 244 loci were left to analyze. I recommend re-running ipyrad with a more liberal threshold for missing data.

Line 168: I assume these analyses are based off the mtDNA, but it would be good to explicitly state this.

Line 171: You should use a coalescent tree prior when analyzing mixed data sets consisting of multiple species and multiple individuals per species.

Line 173: What do you mean by convergence? Did you run multiple independent runs? Do you mean mixing and ESS values?

Line 175: How were node heights determined? Mean heights?

Line 187: Why not simply estimate a ML gene tree for input into mPTP?

Line 191: A bit of semantics, but you may want to use the work genealogy instead of phylogeny, as the former is generally more appropriate when analyzing intraspecific data.

Line 201: This entire section needs to be redone, as I indicated previously. It appears that this is not a species tree analysis, but instead an analysis of the concatenated genomic data. I recommend that the authors familiarize themselves with the numerous methods available for coalescent-based species tree inference. Also, how were data subsets a priori defined for PartitionFinder2?

Line 210: Why were no validation-based species delimitations methods performed (using the genomic data)? This significantly limits the conclusions that can be drawn.

Line 226: Should this be MANOVA?

Line 248: Table 1 is cut-off on both sides.

Line 297: There is no Part B in Fig. 3.

Line 308: The Discussion needs to be toned down a bit, specifically regarding the likelihood of undescribed species. Again, the authors rely almost exclusively on their mtDNA data, which is problematic. Delimiting species based solely off mtDNA is strongly discouraged. I recommend that the authors do a better jobs exploring the genomic data that they collected.

Reviewer 2 Report

The paper from De Carvalho and colleagues addresses in a very clean and understandable way the relevant topic of the presence of cryptic species and the importance of uncovering this cryptic diversity. If neglected indeed, it can result in an underestimation of a species conservation status or inaccurate conservation approach. Despite a formal taxonomic revision is left for future studies, the authors showed the presence of four cryptic “Phrynops geoffroanus” species. The data presented as support look sound and definitely the sampling effort was adequate, as well as the methodologies applied. In conclusion, I am really positive about this paper and I suggest for it to be published in its present form, of course after addition of the Gen Bank accession numbers.

Just something small I noticed:

• In discussion, line 332 “in more recent” is repeated twice
• In References many species names are not in italic.

Reviewer 3 Report

This study assembled mitochondrial (cyt B and COI), nuclear (ddRAD), and morphological data to examine variation contained within Phrynops, a genus of south american turtles that are in need of additional systematic work. The paper has several methodological flaws which collectively render the results uncertain. These analyses fail to strongly support the paper's primary conclusion about the existence of cryptic species present in this group. I outline these concerns below.

Major concerns

The data are underanalyzed for the question the authors seek to address. In particular, the study goes to the trouble and expense of generating a ddRAD dataset. This contains abundant power to fit coalescent models and test for species boundaries, yet the authors choose not to do this. Instead, the molecular species delimitation analyses rely solely on information from mtDNA. The problems associated with relying on single markers for this purpose are well known and widely discussed in the literature (for both turtles and other organisms), yet ignored here. This is particular concerning given that the topology of the mtDNA phylogeny (fig 1) does not match the topology of the nuDNA phylogeny (fig 2). Specifically, the mitochondrial tree finds that 'cryptic lineage' 4 is sister to 'cryptic lineage' 3, whereas the nuclear tree finds that lineage 4 is sister to the remaining lineages. The nuclear tree would seem to be more concordant with the authors' morphological results (fig 3), yet is ignored in favor of species delimitation based on mtDNA data.

Further, the species delimitation analyses that are employed here are all variations on the same theme. These methods rely on the distribution of branch lengths among sampled individuals and attempt to find two modes in this distribution, one that corresponds to the short branches that occur among conspecific samples and the other corresponding to longer branches that occur throughout the tree. Thus these analyses are doing essentially the same thing, and so their high degree of concordance is unsurprising. Further, these methods are strongly sensitive to sampling, with performance degrading as sampling becomes relatively sparse (as it is here). Sensitivity is left unexplored in this study.

Because these lineages are also (for the most part) not morphologically distinguishable (fig. 3), and the nuclear DNA is not analyzed in a way that brings it to bear on species boundaries, the end result of this species delimitation study is that the authors are merely designating mitochondrial clades as species. The authors fail to show that these lineages are something more than the routine sort of mitochondrial structure that we see in many wide ranging species of turtles.

Beyond the issues with analytical design, the methodological reporting here is less extensive than modern standards and is insufficient to replicate the study. Several analytical decisions are left unexplained. As an example, the 'time calibrated analysis' section doesn't mention the prior settings that were used for any parameters of the model aside from the tree prior and a divergence time calibration. Why were yule priors used for trees? What priors were used on others parameter of the model? Further, the authors refer to a nuclear DNA based estimate of divergence times later in the paper, but there is no mention of how this was done in the methods. Similarly, what do the alternatively colored lineages in figure 2 refer to?

The divergence time analysis employs a single time calibration taken from Near et al. 2005 as the basis for calibrating the molecular clock. Thus the divergence time estimates rest solely on this data point taken from another paper. The field now recognizes that legacy calibrations such as this should be avoided when possible. The divergence time estimates reported here are also substantially older than what other recent studies have found. For example, the divergence time between Platemys and the remaining samples is ~60 mya, a little less than twice as old as that found in the most recently published divergence time analysis of turtles (Thomson et al. 2021 PNAS). If the authors choose to stand by this analysis, it would seem that some discussion of how their results fit into the wider literature is needed. That said, I would encourage the authors to redo the analysis employing more reliable methods to do so.

Later in the paper, the authors note that their nuDNA estimates of time are much younger (one third as old) than their mtDNA based estimates. The discussion explains this discordance by invoking both hybridization and the difference between the coalescence times of gene trees versus the divergence time of species. Neither explanation would credibly lead to mtDNA divergence times that are 3 fold larger than found in the nuDNA. Further, both of these assertions are testable with the data the authors have in hand, but this is not done. The authors might also check these results by checking their marginal estimates for substitution rate from these parameters. Are these biologically realistic? These estimates don't seem to be reported anywhere in the paper (I apologize if I have missed them), so it isn't possible for readers to check for themselves.

Overall, the paper falls short of establishing that cryptic species level diversity exists within this lineage of turtles. The study does establish that some mitochondrial structure exists within the species, which is a useful advance for this group of turtles, but should not serve as the basis for taxonomy.

Minor issues:

29 - 'one of two most threatened groups of vertebrates' This sentence depends on what we consider a 'group' of vertebrates. I would suggest rewording this more clearly.
33 - 'though' should be 'thought'
63 - the font size of this paragraph is different than the others
80 - again 'most threatened groups' is unclear. Are we restricting our attention to groups at the taxonomic rank of Order? something else?
230 - 'priory' should be 'priority'
page 7 - table 1 is cutoff and unreadable.