I am in support of reversing the reject decision and would like to authors to submit a slightly revised version before recommendation. Please find my comments in the attached file "Memo on Puntin 2024 MS decision YS.dox.   

First and foremost, I want to extend my sincere appreciation to the authors for their diligent work on this manuscript. The revisions to the experimental protocol have notably enhanced clarity, aligning the message more closely with the results.

However, there remain areas where I diverge from the authors' conclusions. A case in point is the section titled "The microbiome of long-term aquarium-reared Galaxea fascicularis," where the authors propose their hypothesis that captivity leads to the streamlining of the microbiome. This terminology, though technically accurate, may be unnecessarily complex. It essentially refers to the simplification of the microbiome in captive-reared polyps compared to those in the wild. The authors attribute this simplification to the more controlled and stable environmental conditions and the reduced structural complexity of the polyp. While this section also delves into the potential advantages and opportunities presented by this simplified microbiome for experimental manipulation and understanding holobiont functioning, it ventures into discussing the influence of host genotype and environmental conditions on microbiome composition, suggesting avenues for further research to explore these relationships.

However, without a direct comparison of both the microbiome and genomes of the hosts with wild corals, these assertions remain highly speculative.

A reviewer has proposed an alternative hypothesis, which I find more compelling: that the 10-14 days of captivity sufficiently impacted and weakened the bacterial community associated with symbiotic Red Sea polyps to make the effects of bleaching barely perceptible. This idea gains support from the significant presence of a putative coral pathogen (Alteromonas spp.) within the core microbiome of captive Galaxea. Unfortunately, the authors have already dismissed this notion (Line 349), arguing that the reduction or simplification of the microbiome is not an issue associated with captive corals' simplified microbiomes.

Both hypotheses stem from the observation that coral microbiota is simplified in captivity but approach this from different angles. However, without direct comparison data with wild corals and measurements on inputs such as microbiota associated with the corals' diet, etc., it is challenging to ascertain which hypothesis holds greater validity.

Given these circumstances, I anticipate difficulty in crafting a letter of recommendation unless I am personally convinced of the validity of the interpretations drawn from the study's results. I thereby regret to say that despite recognizing the authors' commendable efforts and the significant amount of work they have invested in revising the manuscript, I find myself unable to wholeheartedly recommend the article for publication.

Sincerely,

Cédri Hubas

I trust this letter finds you in good health.

I, along with two different reviewers, have had the opportunity to thoroughly review your study and provide feedback on your submission. Reviewers have articulated several concerns about your preprint, and I wholeheartedly concur with their assessments. The reviewers have highlighted issues such as the relatively low level of replication and the lack of clarity in how measurements were replicated. Additionally, Reviewer 2 has offered valuable insights regarding sequencing and assignment.

The primary concerns raised is about the preliminary nature of the study. While your research presents intriguing insights into the core microbiota associated with the Galaxea fascicularis coral model, the methodology used appears to hinder the generation of clear, conclusive results. The abstract, for instance, implies an expectation of a decisive conclusion regarding the impact of bleaching on the bacterial microbiome of G. fascicularis. However, due to various issues such as the limited number of replicates, sampling from different locations, analysis in different laboratories with slight yet seemingly significant variations in rearing methods, and the absence of comparisons with natural colonies (as pointed out by Reviewer #2), the results come across as over-interpreted. Thus, in my opinion, the study's validity and potential impact must be significantly enhanced with additional results.

After a comprehensive review of your work, I have arrived at the conclusion that I am unable to recommend it for publication in its current state. Below, you will find specific comments that I provide in addition to reviewers comments. Given the methodological limitations, a thorough revision may require the inclusion of additional results.

I cannot make assumptions regarding your ability to supply the requested additional data, so I have opted to request a significant revision rather than an immediate desk rejection. If you are confident in your capacity to furnish additional results and address the queries raised by the reviewers and myself, kindly submit a revised edition of your work. In the event that this proves unfeasible, you will be given the option to withdraw your submission from PCI Microbiology.

Specific comments : 

Materials & Methods:

Experimental Design: The experimental design in your study appears to be quite complex, but it is not sufficiently explained. The number of replicates is unclear, which is a critical aspect of any research study. For instance, in the section titled "Sampling for microbial analysis," you mentioned that "n = 15" for both bleached and symbiotic polyps, but it is not clear how this number was determined. Furthermore, the number of polyps collected seems inconsistent with the mentioned number.

Fig. 1: The statement in Fig. 1 that "Alpha diversity remained similar between symbiotic and menthol-bleached samples across all diversity and richness indices tested" is contradicted by the significant difference in Shannon and Simpson indices in RS1 (Red Sea colony #1). This contradiction should be addressed and clarified.

Results:

Fig. 2A and PERMANOVA: In Fig. 2A, the microbial communities from the Red Sea and Hong Kong colonies appear to be very similar, raising doubts about the significance of the PERMANOVA results. It is essential to reconsider this analysis and possibly perform ANOSIM. Considering the clear heterogeneity of multivariate dispersion in Fig 2A, I doubt that betadisper (PERMDISP2) gave a p-value > 0.05.

Discussion:

The main takeout is that bleaching induce a very different response in bacterial communities in « HK » compared to « Red Sea ». This is probably linked to the fact that HK and Red Sea experiments were conducted in different places with slightly different conditions. Unfortunately, it is impossible to test the laboratory/feeding procedure/aquarium effect because this factor has not been replicated which makes it difficult to draw a conclusion. This limitation should be emphasized to provide a more balanced interpretation of your findings.

Conclusion:

The conclusion section in your paper appears to contrast with the abstract. The abstract fails to clearly convey that the difference between bleached and untreated communities is apparently due to stochastic factors. Instead, it suggests "destabilization and loss of structure of the communities," which comes across as vague and overly wordy.

I hope you find these comments helpful in improving the quality of your research.

Sincerely,

Cédric Hubas