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The manuscript has been much improved and I agree with Reviewer #2 that the interpretation of the data is now adequate. Happy holidays.
I'm happy with the changes made, outlined in the rebuttal letter, leading me to recommend this article for publication. Given the impossibility of an SBV-only treatment, I agree that the changes made in reporting, and additional sentence highlighting coinfective dominance of SBV, are adequate improvement. The further qualification of your infection dynamic interpretation as highly speculative is adequate, and indirectly emphasises the (rightful) possibility of alternative explanations. In my view, exploration of them is not necessary for this manuscript's publication in PeerJ.
Whilst not explicitly stated, it is now clear to readers from the information in the study that SBV infection in A. mellifera is almost universally additional to DWV circulation within a colony - hence the lack of SBV-alone injection observations. This exclusively coinfective ecology of SBV could, speculatively, be the evolutionary driver leading to its observed dominance over DWV. This line of reasoning makes the manuscript of increased interest, but admittedly this study is not the place for its discussion.
I would also like to apologise for my oversight in not properly checking figure legends for sample sizes, when claiming they were not present in the manuscript.
I look forward to future work on this following the manuscript's publication. I believe there is substantial potential in this DWV-SBV system as a fruitful line of both A. mellifera ecology and pathogen evolution research.
This is an interesting study but there is perhaps a bit too much speculation laid out in the abstract and title, especially because your results are based on gene expression only. For example, you do not actually test whether the expression of the AMPs or melanisation pathways alters the ability of these viruses to be transmitted. Please address the concerns of the reviewers, especially reviewer #2 (re: SBV inoculations alone and conclusions therein). I should note that although reviewer #1 did not include much detail in their evaluation, your manuscript was carefully vetted by me, the handling editor.
35: deformed wing virus -> at least ‘deformed’ is written with a capital first letter
37: Please change the italic reference.
40-41: Although DWV has a limited genetic diversity, there a some hotspots like Lp. This gene is very diverse, even in one apiary (Ravoet 2014).
49-50: It might be relevant to discuss the severe impact of the Asian SBV serotypes on the development of Apis cerana.
76: virus preparations stored -> virus preparations were stored
150, 344: Mention the databank for this accession number, like GenBank.
69: It is unclear to me if the virus preparations were checked for viral contaminants since multiple viruses can be present in one honeybee?
Indentations below a title are not necessary.
Overall the article is well written, and frames the study succinctly in terms of honeybee decline. However, the introduction fails to properly introduce the later discussion of viral evolutionary strategy which forms the link between the scale of this study and its relevance to honeybee declines. This will be particularly important if recommendations below on expanding the discussion of adaptive virulence are taken on board.
Figures are clear, informative, and do an excellent job of expressing all necessary information.
The experimental concept is certainly novel enough to warrant publication in PeerJ, hypotheses are clearly identified and there is no doubt about the clarity of the proximate research questions. However there are problems with design, implementation and reporting of the experiment.
While the treatments are suitably controlled – I am particularly pleased to see the use of both a saline treatment and an inactivated viral treatment - there is a conspicuous absence of an SBV-only pupal injection treatment (Lines 89-95, 263-291, Fig 4). This omission needs to be rectified, or as a minimum adequately justified; it currently leaves this aspect of the study incomplete and not is addressed anywhere in the text. This missing treatment casts doubt on some of the claims made in the discussion (further comments below).
Additionally, there appears to be nowhere in the manuscript or supplementary information details as to how many larvae and pupae were treated. This absence of sample size is a basic oversight which should have been addressed before submission. Alongside no reporting of degrees of freedom for the t-tests undertaken in figures 3 and 4, this is not acceptable for publication.
The suite of molecular methods and subsequent bioinformatics used to characterise the responses to the treatments are thorough, well analysed, and presented clearly.
However, care should be taken that all acronyms are stated in unabbreviated form first, even if common across the discipline:
Line 119 – ‘NGS’ never stated as next-generation sequencing
Given the unaccounted for omission of the SBV-only injection treatment, a questionable assertion is made in discussion: Lines 295 – 297
“The pupal injection experiment further confirmed that hymenoptaecin and defensin-1 are up-regulated in the insects with high SBV levels.”,
summarise this. I don’t believe this claim can be made without an SBV-only injection treatment, particularly as there are disparities between the oral and injection infection results for DWV (Lines 286-288). Much of the remaining discussion relies on this contentious claim, and ultimately the conclusions drawn are not convincingly supported by the data as a result.
Setting the above problem aside, discussion of the alternative mechanisms for SBV causing up-regulation are fairly assessed, with clear steps taken (Fig. S1) to address competing explanations. The nuanced discussion in this paragraph (Lines 309 – 327) sets a clear mandate for further study on how to detect direct vs indirect effects mediated by SBV pathogenesis.
The framing of the observed differences in transcriptome response to DWV or SBV infection in an adaptive virulence context (Lines 328-352) is commendable, however I would recommend this aspect of the discussion to be refined and extended. It is not clear why, when horizontal transmission has been shown as possible in both viruses, they have diverged in strategy. There is no mention of SBV as a potential obligate killer, which is what Fig. 5 portrays. More considered reasoning and acknowledgement should be shown of the positive feedback between high pathogenesis leading to transmission principally following host death, and the establishment of this main mode of transmission reducing remaining selective constraints on pathogen virulence.
As a recommendation, this aspect of the discussion would substantially improve the paper if it also framed the observed dominance on the transcriptome of SBV over DWV in the context of co-infection. It is clear the authors are suggesting opposing transmission strategies between SBV and DWV, and considering co-infection was administered in the study it is again conspicuously absent from the discussion. This point in particular highlights the study’s potential relevance to the originally introduced problems of honeybee decline in the face of virulence pathogens.
Overall I am keen to see this study live up its potential, and can readily recognise the contribution of the manuscript to the wider literature, should the recommendations be taken on board. The main concern is the conspicuous absence of a SBV-only injection treatment. Addressing that missing aspect, in addition to the other comments on sample size and discussion emphasis, will make for a very compelling article. However in its current state, I do not consider this submission of publishable quality.
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