Review of 'Serotonin is required for pharyngeal arch morphogenesis in zebrafish'

S. Bashammakh et al.’s study nicely demonstrates the requirement of serotonin (5HT) in differentiation of the pharyngeal arches. They use a very logical series of experiments to show such a requirement for serotonin and pathway members. First the authors show localization of serotonin, tph genes (encode for enzymes needed for the synthesis of serotonin), and serotonin receptor. This is followed by knockdown of tph2 and inhibition of serotonin receptors. An analysis of neural crest and jaw cartilage in the inhibitor treated and tph2 morphants indicates a potential role in pharyngeal development. This is a very valuable piece of work and makes a nice contribution to the field of craniofacial development.

Level of importance:

Is the publication of relevance for the academic community and does it provide important insights? Does the work represent a new approach or new findings in comparison with other publications in the field?

I would rate this article 3.5 stars for level of importance. This article investigates the role of serotonin in pharyngeal arch morphogenesis. However, such a role of serotonin has been shown in mice and Xenopus and thus is not a 100% novel finding. Despite this, they do make an important addition by showing that this is likely a conserved mechanism by using zebrafish. Further, they provide additional details of the molecular mechanism by 1) using serotonin receptor antagonist to show the role of the receptors and 2) to reveal a role for tph genes.


Level of validity:

Is the hypothesis clearly formulated? Is the argumentation stringent? Are the data sound, well-controlled and statistically significant? Is the interpretation balanced and supported by the data? Are appropriate and state-of-the-art methods used?

The hypothesis for this paper is that serotonin plays a role in the development of the pharyngeal arches in zebrafish. This hypothesis was clearly formulated and investigated in a clear, stepwise fashion. The data is presented clearly. However, I have a number of concerns about the methods and interpretations.

1) A major concern about this study is that the numbers of embryos used to draw conclusions is not high and sometimes not even stated. For example, I am concerned by the number of subjects used for the initial characterization of 5-HT expression: the methods section says “a total of 10 embryos from different stages” which implies that 10 embryos were used for the 5 stages analyzed, for a total of 2 embryos per stage. If this is the case, this is too few embryos for this analysis and thus would lead me to question the results. For the remainder of the studies, the number of embryos used is not mentioned, again leading me to question the validity of the experiments.

2) Quantification of the data is poor. There are no graphs presented to support the study of the tph morphants. For example, the penetrance of the phenotype is not mentioned (as well as if the experiment has been duplicated) suggesting that all the embryos are identical, this is rare in morpholino experiments. Also the interpretation of the in situ markers (sox9a and dlx2a) could have been strengthened with some measurements or quantitative PCR.

3) Another major problem is that it is not clear why the time points were chosen for expression analysis and the interpretation is not clearly written. I don’t understand why tph genes are not present at least near the pharyngeal arches. I am lead to the impression that serotonin diffuses from the brain or pineal gland to act on the pharyngeal region. It could also be that tph2 for example is expressed in the arches at different times not examined in this study. It was presented that the receptor antagonist is most effective after 2 days and therefore expression analysis over this time period would have made more sense.

4) The connection between tph2 and the serotonin receptors are not strong. The cartilage defects shown from the tph2 knockdown and ritanserin treatment don't look that similar, especially considering the angle of the joints. Synergy experiments between the two strategies would have more clearly demonstrated a connection.

5) In the tph2 knockdown experiments there is no assessment of toxicity of the morpholino, usually a p53 MO is coinjected or minimally an apoptotic assay used.
I would rate this paper 3 stars for validity because the hypothesis was clearly formulated and investigated, however there were a number of major concerns about the quality and interpretations of the data.

Level of completeness:

Do the authors reference the appropriate scholarly context? Do the authors provide or cite all information to follow their findings or argumentation? Do they cite the all relevant publications in the field?

To my knowledge the authors cite relevant scholarly content. I would rate this article 5 stars in this category.

Level of comprehensibility:

Is the language correct and easy to understand for an academic in the field? Are the figures well displayed and captions properly described? Is the article systematically and logically organized?

This article is very well organized in terms of the presentation of the data and would give it 4 stars. The language is correct and easy to understand. However, at times the analysis of the data feels like a digression from the results, this could be clarified. The last conclusion made by the authors does not flow well with the rest of the paper. I feel like this conclusion should have been explored in greater detail if it was to be included. Perhaps it was not explored more because of space constraints; if that was the case then it should not have been included as it does not strengthen the paper in its brief form.