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Dear Dr. Cerca and colleagues:
Thanks for revising your manuscript based on the concerns raised by the reviewer. I now believe that your manuscript is suitable for publication. Congratulations! I look forward to seeing this work in print, and I anticipate it being an important resource for groups studying ghost-worms and cryptic species complexes. Thanks again for choosing PeerJ to publish such important work.
Best,
-joe
[# PeerJ Staff Note - this decision was reviewed and approved by Nigel Andrew, a PeerJ Section Editor covering this Section #]
Dear Dr. Cerca and colleagues:
Thanks for revising your manuscript. The reviewers are very satisfied with your revision (as am I). Great! However, there are a couple issues to still address and a few minor edits to make. Please address these ASAP so we may move towards acceptance of your work.
Best,
-joe
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The authors did a great job in addressing all the comments of the reviewers, not only mine. Well done. I am sure it will be an interesting paper for several readers.
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I am very please with the response to my queries. No further comments.
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There was considerable improvement to the manuscript in response to reviewers' concerns and I believe it is much better now. That said, the paper could benefit from revision of a few points. Here I start by making some comments that have been apparently overlooked during the first round of reviews and then I make a few suggestions based on the current version of the manuscript.
One of them was a problem already in the first version (model comparison by likelihoods), but the figure in the first version had an unlabelled axis and it was unclear whether this was the case. Now that it is clear, I suggest to use the likelihoods to calculate AIC instead of comparing models by likelihood directly. AIC scores should be comparable across models, but likelihood is not due to the different number of parameters. If anything, I believe this will make the main argument stronger, decreasing support for models including migration in relation to models with migration.
Before pointing out parts to be revised, I would like to commend the authors for the careful revision. While it is clear that great care was taken to address major comments, it seems some of minor issues that I pointed out in the first round were neglected, so I rephrase them here:
1 - I still do not understand why samples are split in A0 and A1 in Figure 2 if alleles are unphased. Whether an allele is marked as "0" or "1" is arbitrary because of the lack of phasing, and therefore grouping them this way makes no sense. I would think that a phylogeny based on the consensus sequence for each individual would be more appropriate.
2 - "Maps, Google" is still in the references. I would suggest reviewing references more broadly prior to publication. For example, there are two preprints cited and by now they might have been published already.
3 - "bad apple" is still mentioned in Supp. Table 2 but not defined in text. In the description of the method to minimize missing data one can guess these are the samples with >45% missing data that have been removed, but since the term "bad apples" is used in the supplement it should also be explicitly defined in the main text (or removed from the supplement).
In addition to those, I have a few comments on this version of the manuscript.
1 - Not sure if I am the one who failed here, but I could not find and download fastsimcoal files that should be in the supplement. Please make sure they are provided in the final version (e. g. together with code) to ensure reproducibility.
2 - While the authors disclosed the mutation rate used in the response to reviewers, it is not mentioned in the text. This is important, since the number of generations estimated and discussed depends on mutation rate. For example, the authors mention that species of Stygocapitella have one generation per year, which is as important as mutation rate to interpret how this relates to actual time scales. I would suggest adding it as a short sentence to methods, not only the supplement.
3 - While in the response authors mention not using a minimum allele frequency criterion for estimation of Tajima's D, it is not clear in the text when a maf was used or not. The only time maf is mentioned is in line 216, and it seems implicit that this criterion applies to all downstream analyses. If this is not the case (as seems to be from the response to reviewer's comments), it should be stated explicitly.
4 - Now that it is clear that the y axis in Figure 6 is likelihood, this reveals a problem. Model comparison in a likelihood framework needs to take into account the number of parameters, since a simpler model is preferable to a more complex one if they have the same likelihood. There are different ways of accounting for number of parameters, but the Akaike Information Criteria (AIC) is one of them and widely used in the context of fastsimcoal. AIC = 2*k - 2*L, where k is the number of free parameters (i. e. the number of parameters in the *.est file of fastsimcoal) and L is the log-likelihood. After calculating the AIC for each model, these can be directly compared and the best model should have the lower AIC. There are several tutorials available, I found one of them here, for example:https://speciationgenomics.github.io/fastsimcoal2/
I suspect that after comparing models by the AIC the model with no migration will be favored in relation to others, making the argument in the paper stronger.
5 - line 280, "module as asymmetric" should be "modelled as asymmetric".
6 - There are weird characters following numbers in the paragraph starting in line 294
Dear Dr. Cerca and colleagues:
Thanks for submitting your manuscript to PeerJ. I have now received three independent reviews of your work, and as you will see, the reviewers raised some concerns about the research. Despite this, these reviewers are optimistic about your work and the potential impact it will have on research studying ghost-worms and cryptic species complexes. Thus, I encourage you to revise your manuscript, accordingly, taking into account all of the concerns raised by both reviewers.
There are many suggestions, which I am sure will greatly improve your manuscript once addressed.
Importantly, please consider comments about the rationale. Also, ensure that the phylogenetic methods are robust and account for missing data and paralogy.
I look forward to seeing your revision, and thanks again for submitting your work to PeerJ.
Good luck with your revision,
-joe
[# PeerJ Staff Note: Please ensure that all review comments are addressed in a rebuttal letter and any edits or clarifications mentioned in the letter are also inserted into the revised manuscript where appropriate. It is a common mistake to address reviewer questions in the rebuttal letter but not in the revised manuscript. If a reviewer raised a question then your readers will probably have the same question so you should ensure that the manuscript can stand alone without the rebuttal letter. Directions on how to prepare a rebuttal letter can be found at: https://peerj.com/benefits/academic-rebuttal-letters/ #]
The manuscript represents one of the fist comprehensive studies of gene flow between cryptic taxa in a species complex of marine microscopic animals. Meiofauna is one of the groups of animals where DNA sequences are often used to delimit taxonomic units, and this study goes a step further in attempting to understand the level and timing of gene flow to explain morphological similarity. The analyses are appropriate and provide supported results for the inference. I wish that such approach could become the standard in meiofauna and I congratulate the authors for their work.
The experimental design is fine
the findings are highly novel and relevant.
I have a series of comments to improve the strength of the message, removing weaknesses or ambiguities. These may be just subjective opinions, but consider that also other readers may have the same doubts.
1. What I do not find completely convincing is the connection between past gene flow and morphological similarity in cryptic species. The fact that gene flow exists does not explain the reason for morphological similarity. There are several examples among plants and animals, even meiofauna, where extensive gene flow and hybridisation do not preclude the possibility to identify species morphologically. This part of the rationale should be rephrased to provide convincing statements, or should be removed. I would opt for its removal, given that it does not provide more interest to the results and it only makes the rationale less convincing.
2. Another part of the rationale that is not supported is in the first paragraph of the discussion (and in parts of the introduction), where the search for the reason for the morphological similarity is not due to bottlenecks or recent admixture, and thus it is stated to be “in line with an incomplete lineage sorting scenario”. The ILS scenario is thus supported in the absence of the other causes, omitting other potential explanations. The presence of ILS is not even demonstrated, because it seems that hybridisation could be the reason for gene sharing. Thus, if hybridization exists, no ILS can be supported. Maybe a test to support whether ILS or hybridization is present should be included. Something along the line of the statistical rationale used by Joly et al (https://www.journals.uchicago.edu/doi/full/10.1086/600082) may do the job. In any case, even after such test, the connection with morphological similarity is weak. Only a comparison with the level of gene flow between closely related species groups of taxa that are morphologically distinguishable and diverging at the same time could be used to identify the reason for morphological similarity in cryptic taxa.
3. Overall, the idea is great, the data and the analyses surely worth, but the rationale to fit the results in the idea of searching for a reason for morphological similarity weak, and not necessary.
Other issues
4. The idea of cryptic species being taxonomic artefacts is reported in the abstract and in the introduction without any further explanation. My suggestion is to (i) expand the idea and clearly explain it in the introduction, given that most readers will disagree on it, and to (ii) remove it from the abstract, where it may represent an ambiguous weakness for several readers.
5. Also the idea that cryptic species are overlooked, on line 46, is not unambiguous. If anything, most taxonomic studies nowadays deal with DNA sequences and make integrative taxonomy the rule and not the exception. I understand that this is only my subjective opinion, based on the organisms I work with; yet, there is no reason to upset some readers with unsupported statements and I would suggest to remove the phrase ‘yet overlooked’ on line 46.
6. The nomenclature of the species complex is not always clear. For example, on line 89, it is reported as “The Stygocapitella species cryptic complex”, which does not make much sense, because (i) it does not report the name of the species complex but only of the genus, and (ii) the order “species cryptic complex” is not understandable. The same problem of unclear nomenclature appears already in the title and in the abstract: a complex of cryptic species cannot be identified by the name of a genus. One genus may contain several easily distinguishable species and also several species complexes, which are all named individually usually by using the name of one of the species in the complex. The problem is clearly seen in the sentence on line 89, where 11 species with 4 morphotypes are mentioned, revealing that not only one, but 4 complexes of cryptic species, which cannot be distinguished using morphology alone, exist in the genus. Please, remove this ambiguity in the terminology and clarify what the complexes are.
7. The hypotheses at the end of the introduction are unclear and unsupported. H1 bottlenecks and founder effects should not only provide morphological similarity; bottlenecks and founder effects, by reducing genetic variability within each population of each species, maximise differences between populations and between species, which is the opposite of what is stated. It is true that bottlenecks reduce genetic variability, as stated in the discussion on line 512, but bottlenecks are one of the traditionally accepted mechanisms to have genetic diversity between populations, quickly leading to speciation, again in the opposite direction of what is assumed in the hypothesis. Think of the bottleneck and founder effects on islands, quickly leading to morphological differences between the island and the source populations. Please, clarify the rationale for this hypothesis. H2 implies that hybridisation makes species more similar, but there are lots of examples of complexes of hybridising species that can still be distinguished morphologically, for example in plants but also in other microscopic aanimals where evidence of mitonuclear discordance has been found. H3 could be OK, but the fact that ILS is present should be clearly tested and not assumed.
8. On line 86-87, the sentence “Very few biogeographic and systematic studies, let alone evolutionary studies, have thus contributed to the discussion” is then followed by a list of 6 references (several from the authors), making the sentence not so supported. A list of 6 references cannot be considered to represent “very few” studies, considering that several other studies have not been mentioned. Especially in meiofauna, the use of DNA taxonomy in the study of biodiversity in all its aspects (including biogeography and evolution) has a long history and several readers may not agree on the sentence.
9. Given that the study is on species, it would be better to use zoological nomenclature according to the strictest rules in taxonomy, reporting species authorship at the first citation of a species in the main text, taking care of reporting the correct use of parentheses.
10. The chapter starting with the title on line 159 on “Species delimitation” does not describe any method of species delimitation but only the “multi-marker phylogeny”. Either change the title or include a description of the methods that are used for species delimitation.
11. In the same chapter, a sentence should state whether ITS was present with double peaks or not, and how the double peaks were treated. Check this method for double peaks in ITS in species delimitation: https://besjournals.onlinelibrary.wiley.com/doi/abs/10.1111/2041-210X.13454. I am not suggesting to use haploweb, but I only want to point out that the reader may need to know what happened to the double peaks in ITS1.
12. Line 359: ‘taxa’ does not seem to be the correct term, as the idea refers to ‘individuals’
13. The long discussion on pooling individuals for RADseq seems out of place. Please, shorten it considerably. It is already convincing that the study managed to get good genomic data from single animals through WGA. Also the caveats due to WGA should be shortened, and especially moved at the end of the discussion. It would be much better first to discuss the biological implications of the results, and then only later introduce the potential problems. Starting the discussion with problems seems to distract the reader. Just a minor point: WGA works also for rotifers, which are much smaller than the analysed anellids (https://www.sciencedirect.com/science/article/pii/S0960982216000816; https://journals.plos.org/plosbiology/article?id=10.1371/journal.pbio.2004830).
14. The discussion in the part on line 521 is weak. ILS and hybridisation can be distinguished statistically (https://www.journals.uchicago.edu/doi/full/10.1086/600082) and the manuscript remains too ambiguous on this point, stating that admixture could be due to one of the two processes, but then without testing which is more likely.
15. In the same part of the discussion, the speculation on sympatric and non sympatric populations is also weak: if the estimates are correct, gene flow can happen every thousands of years, meaning that animals from different populations have the time to move from one population to the other.
16. The selection of references is a bit too much biased towards the production of the authors. Whereas I would say that it is a good option for the discussion, having too many references from the authors in the introduction may leave the impression that only the authors care about this topic, with no broad interest. This is not true, and several studies on cryptic species, their origin, and their biogeography exist in the meiofauna, other than in anellids.
17. The choice of colours representing the three species in the figures is not the best one: two of the three species will not be clearly seen by several readers with colour vision impediments (green and orange may be mixed up). Choose a set of three easily distinguishable colours to be more inclusive.
18. The English language is rather good, but please consider a careful revision, in order to remove very minor problems such as:
- Single comma between subject and verb (e.g. on line 42).
- No hyphens are allowed for adverbs ending with –ly (e.g. on line 49, 61, 62, etc.); this is called a hypercorrection, because no ambiguity is possible with such adverbs and thus the hyphen is redundant. The text is already ambiguous in the use of such hyphen, because in some instances the adverbs are already reported without the hyphen (e.g. line 91).
- Hyphens are not used consistently also in other phrases, for example “missing-data” on line 274 should not have the hyphen. Please, carefully check the use of all the hyphens in the text.
- The term ‘specimen’ is used ambiguously: strictly speaking, ‘specimen’ is a representative individual or part of it, stored in a collection, whereas in the manuscript it is used with the meaning of a single individual. I guess that the animal is completely destroyed by the DNA extraction, and thus the ‘specimen’ is lost and cannot be considered a specimen anymore. In addition, the phrase ‘individual specimen’ is a tautology. The misleading use of ‘specimen’ is only a minor problem, but for entomologists and other readers who work in museums the manuscript will seem weird. Thus, there is nothing to gain by using ‘specimen’ instead of ‘individual’, which will make all readers happy.
- ‘a loci has’ should be ‘a locus has’.
- ‘These statistics consists’ should be ‘These statistics consist’.
- ‘which’ is used for both restrictive and non-restrictive clauses, but at least one instance of the use of ‘that’ instead of ‘which’ are present (e.g. line 485) and should be removed for consistency.
- On line 368, ‘the least amount’ should be ‘the lowest amount’, because amount is countable.
I hope that my comments could be useful to strengthen the impact of the message of the study.
Yours sincerely,
Diego Fontaneto
I think this is an extraordinary contribution to our understanding of the factors that determine the existence of cryptic species, and the current debate of the increasing discovery and the lack of integration into an evolutionary framework as discussed by the authors.
In my opinion the paper covers the most relevant literature published on the subject, it is very well-written and structured and all the hypothesis are very well tested and discussed. No ambiguity I can see from reading this nice piece of work .
On lines 56-64 author present idean on how the discovery of cryptic species is important in terms of biological systematics, but also in other fields in terms of their practical impact, I would suggest to use the example of parasitic organisms, where this fact has been clearly shown at least in two studies (Pérez-Ponce de León and Nadler, 2010 Journal of Parasitology 96, 453-464, and Nadler and Pérez-Ponce de León 2011 Parasitology 138, 1688-1709. .
It is mentioned in the introduction that the genus contain 11 species, although in WoRMS (World Register of Marine Species), only 8 are reported.
The methodological approach to test the hypothesis that morphological similarity among three species of the polychaet Stygocapitella is the result of either bottlenecks, recent admixture or incomplete lineage sorting is sound and actually it is on the state-of-the-art since it uses whole genome data and a vast array of methods currently available.
In my opinion, the question is fully addressed and the conclusions are very clear.
I have a question regarding the use of independent molecular markers. It is mentioned in the results section lns 286-294 that authors compiled a dataset of 4,147 bp, for 4 molecular markers (COI, 16S, ITS1, 18S), and the phylogenetic tree is the result of the concatenated analysis (Fig. 2A), although the sample size for each of them is quite variable, did the authors check for the reliability of presenting a concatenated analysis of the 4 markers?. I think that part of the methodology is very short and not fully explained.
The approach followed by this paper is novel, and points to the use of genome data to fully understand the factors that determine the occurrence of cryptic species in natural systems, including the 11 potential causes outlined by authors on lns 71-82 of this paper.
In my opinion, conclusions are clear and open a clear path to demonstrate with other empirical studies that the processes underlying the morphological similarity among the 3 species of Stygocapitella studied in this work. The analyses left some room for speculation, which in my opinion is well justified.
Very nice piece of work!.
In this contribution, Cerca et al study the population genetics of 3 cryptic and partially sympatric species of the meiofaunal worm Stygocapitella. Based on previous work with a limited number of markers, the 3 lineages were recognized and here they evaluate whether the morphological similarity is a result of recent bottlenecks, continuous gene flow or incomplete lineage sorting. The paper is well-written and figures are informative. The DNA data deposition statement includes raw Illumina reads but not Sanger sequences (maybe it could mention they are in supp table 2 for easy access?). Code is not provided in the current version, which prevented interpretation of some results (see Experimental design)
Given the general lack of knowledge on the diversification of meiofauna and the huge diversity of these animals, this paper is a relevant advance showing how speciation does not necessarily lead to morphological differentiation, and attempting to rule out some of the hypotheses explaining that. The extensive geographical sampling and transparency in presentation of results are also noteworthy. Another important outcome of the study is the presentation of a methodology to work with challenging samples represented by these small animals: some of the reasons for the lack of studies are precisely the difficulty in sampling and applying standard molecular protocols to these organisms.
I believe, however, that some of the results presented in the paper could be artifactual, and more work could be done to demonstrate their validity before publishing. Specifically, despite the efforts to mitigate these problems, missing data could still be affecting the results, the interpretation of coalescent models is problematic, and the data could be further filtered to remove artifacts arising, for example, from paralogy. I believe that rejection of hypotheses 1 and 2 (bottleneck and introgression) could be due to artifacts, and therefore more analyses are needed to demonstrate that this is not the case (or to review the conclusions, if it is). That said, I also believe that all problems can be addressed with the data available, and below I make suggestions for each point.
The research questions are well-defined, but I believe their framing could be improved. Specifically, the end of the introduction seems to suggest that one of the three hypotheses is the cause for cryptic species, when earlier the authors list more processes that cannot be tested with data in hand (for example, stabilizing selection on phenotypes). It is well possible that the three species have not undergone bottlenecks, do not hybridize and do not retain ancestral polymorphisms and yet are morphologically similar. Similarly, finding that ILS exists in this system does not imply that it is responsible for the morphological stasis and other, untested, processes are not occurring (such as stabilizing selection). The authors could acknowledge that more explicitly.
Methods are generally described in detail, but in several instances the authors refer important information to other papers. In some instances (specific comments in minor suggestions below), relevant information could be repeated in this paper. Below I make a few comments on the major points in which methodological choices can impact results:
The parameter files for fastsimcoal are not provided, nor any description of the parameters used. This is important, because the authors use the absolute number of generations to species divergence to rule out some of the coalescent scenarios. It is somewhat unfortunate that fastsimcoal works with absolute numbers instead of coalescent units, since inference of absolute effective population sizes and divergence times is only reliable if there are reliable mutation rates. Since the mutation rate used (and a justification for its choice) is not provided, I believe that direct interpretation of coalescent times in generations is problematic. Therefore, I find the conclusion that there is no gene flow between species unconvincing when models with gene flow are clearly well supported. Moreover, since both ancient gene flow and recent gene flow between s-w were supported, maybe it would be important to add a model with these two migration parameters simultaneously. Finally, it is not clear whether gene flows assumed to be symmetric. If it is highly asymmetric, and assumed to be symmetric, one could be missing scenarios of gene flow with very strong support from the data.
Another important fact for interpretation of results and not thoroughly discussed in text is missing data in the Sanger dataset used to evaluate species identities. It seems that for many samples the data is heavily biased to the two mitocondrial genes. The authors refer to previous work to say that there is no discordance between genes from the Sanger sequencing dataset, but it is not clear if this previous work included the few samples with discordance between datasets found here. Could it be that the labelling of species is only reflecting mitocondrial lineages? In that case, it is possible that rare introgression affecting only a small part of the genome (such as mtDNA) is driving observed patterns, at least in part. Maybe showing trees for each gene, highlighting samples placed "incorrectly" in the concatenated SNP dataset would help in understanding patterns.
Despite all the effort to minimize missing data, it seems that there might be still substantial missing data for some individuals. A table with amount of missing data per sample could help to visualize that. Fig 2A shows a typical pattern when adegenet is used in datasets with large amounts of missing data: samples with large amounts of missing data are pulled to the middle, obscuring patterns. This is because adegenet uses a very simple rule for imputing missing data: replacing these with average allele frequencies. This may be problematic in a sample with substantial missing data (close to 50%, for example), and the differences between MDS (which I assume ignores pairwise missing data) and PCA indicate that this may be a problem.
See, for example, the following reference:
Larson, WA, Isermann, DA, Feiner, ZS. Incomplete bioinformatic filtering and inadequate age and growth analysis lead to an incorrect inference of harvested‐induced changes. Evol Appl. 2020; 00: 1– 12. https://doi.org/10.1111/eva.13122
Moreover, as also discussed in the reference above, it is possible that the dataset includes problems such as paralogy, which can further obscure patterns and affect inferences. The text does not mention a filter for paralogy, for example.
To mitigate both problems, I recommend using genotype likelihoods instead of called genotypes for doing the PCA. This is implemented in PCAngsd:
Meisner J & Albrechtsen A. 2018. Inferring population structure and admixture proportions in low-depth NGS data. Genetics 210: 719–731.
The same program also provides a method for testing sites for Hardy-Weinberg equilibrium while considering population structure, which is a powerful method to remove artifacts such as paralogy:
Meisner J & Albrechtsen A. 2019. Testing for Hardy–Weinberg equilibrium in structured populations using genotype or low-depth next generation sequencing data. Mol. Ecol. Resour. 19: 1144–1152.
Implementing these would require some changes to the workflow in the paper, notably not using genotypes called by stacks but rather using stacks loci only to produce a reference "genome" onto which raw reads are mapped and then used as input to ANGSD (http://www.popgen.dk/angsd/index.php/ANGSD) followed by PCAngsd. Given the nature of the dataset, I believe it is important to use a method less sensitive to missing data. The usage of genotype likelihoods would decrease the amount of missing data by allowing lower-coverage loci, the PCA would be estimated without the bias mentioned above and problematic loci would be filtered. This might have significant consequences for results presented.
A final point that I believe deserves attention is the choice to filter SNPs with minimum allele frequency below 0.05. Given the sample sizes used here, it would be possible to detect alleles with frequencies lower than that, an I am wondering if ignoring low-frequency alleles has an effect on statistics such as Tajima's D. If this is the case, the conclusion that populations did not experience bottlenecks could also be an artifact. I would recommend testing the effects of a lower theshold, perhaps 1/N, where N is the number of samples sequenced.
The discussion is well-written. However, given the concerns raised in Experimental Design above, I believe that a careful discussion of the validity of the findings can only be done after concerns about artifacts are addressed.
Minor suggestions
throughout the text: species names are not italicized
line 110 - I believe "Maps" is not the last name of "Google Maps", please revise this reference
line 180 - even though a reference on best practices is cited, the authors could briefly comment on which criteria were used to select -M 3 and -n 3. Why was this considered the best combination?
line 190 - what is PeerJ policy for citing unpublished data?
line 450 - "stochastic biases" - I find this construction confusing, not sure if by this the authors mean random or systematic errors.
Supplementary Table 2 - The legend mentions that "bad apples" are defined in the main text, but no reference is made there.
Fig 2 - what is A0, A1? Are these the concatenation of the two alleles? If this is the case, since RAD loci are generally unlinked, I do not think that considering them as separate terminals makes much sense. Maybe using the consensus for each sample?
Additionally, it is not clear what "shared pairwise data" means. Is this the average number of loci shared with other samples? Why is it different for A0 and A1 for a given sample?
fig 6 - The figure is missing y axis label. Moreover, is this really likelihood, or is this AIC? I believe this may be the AIC, since one would expect the likelihood to increase with more model parameters.
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