Relative abundance of nitrogen cycling microbes in coral holobionts reflects environmental nitrate availability

Recent research suggests that nitrogen (N) cycling microbes are important for coral holobiont functioning. In particular, coral holobionts may acquire bioavailable N via prokaryotic dinitrogen (N2) fixation or remove excess N via denitrification activity. However, our understanding of environmental drivers on these processes in hospite remains limited. Employing the strong seasonality of the central Red Sea, this study assessed the effects of environmental parameters on the proportional abundances of N cycling microbes associated with the hard corals Acropora hemprichii and Stylophora pistillata. Specifically, we quantified changes in the relative ratio between nirS and nifH gene copy numbers, as a proxy for seasonal shifts in denitrification and N2 fixation potential in corals, respectively. In addition, we assessed coral tissue-associated Symbiodiniaceae cell densities and monitored environmental parameters to provide a holobiont and environmental context, respectively. While ratios of nirS to nifH gene copy numbers varied between seasons, they revealed similar seasonal patterns in both coral species, with ratios closely following patterns in environmental nitrate availability. Symbiodiniaceae cell densities aligned with environmental nitrate availability, suggesting that the seasonal shifts in nirS to nifH gene abundance ratios were probably driven by nitrate availability in the coral holobiont. Thereby, our results suggest that N cycling in coral holobionts probably adjusts to environmental conditions by increasing and/or decreasing denitrification and N2 fixation potential according to environmental nitrate availability. Microbial N cycling may, thus, extenuate the effects of changes in environmental nitrate availability on coral holobionts to support the maintenance of the coral–Symbiodiniaceae symbiosis.


Recommendation?
Accept with minor revision (please list in comments)

Comments to the Author(s)
The authors have presented an insightful and well-written manuscript which is almost ready for publication. I only have a list of minor issues, which mostly concern the statistical part of the paper.

Methods:
Line 152: what is this conversion factor based on? I do not see sources. Is this based on the spectral light quality in situ?
Results: Supplementary Table S1 lists no interactive effect of species and season on gene ratios. Thus, the authors can only resort to testing differences between seasons for both species combined (i.e. averaging the data from both species for each season). However, as shown in figure 1B, the authors have tested the means of the different seasons against each other per species. Splitting the data into both factors and doing pairwise comparisons like this can only be justified when the PERMANOVA first yields a significant interaction. I recommend testing the various seasons against one another without splitting the data into both species (i.e. performing a post-hoc test to follow up the significant main effect of season). Indeed, this is what the authors have done and described in lines 205 to 207. I would therefore change the pairwise comparisons in figure 1 to reflect these lines. Lines 194 to 198 should be removed as these suggest an interactive effect, which is not there. I would first report significant effects and then report the ratios which significantly differ, with species pooled. Supplementary table S2 should not list parts A and B, but should include C, where the species have been correctly pooled (and the rest of the table, of course). Interestingly, the authors did pool species for their correlations as described in lines 259 to 261. I agree with this approach, by the way. I hope the pairwise tests account for inflation of the familywise error (i.e. the p-values were corrected to compensate for multiple comparisons. Was this why you did parallel Monte Carlo tests)? I would make this issue clear in the M and M, because p values can be adjusted or a Bonferroni correction (with alpha / number of pairwise tests) can be done. In relation to this: Figure 1C is correctly done as there is a significant interactive effect for cell densities. Table S2 details pairwise comparisons for environmental variables (f to o), but I do not see a main PERMANOVA table with season as factor and a corresponding pseudo-F, which should be presented before performing pairwise (post-hoc) comparisons, correct? If so, table S1 should be expanded accordingly. Indeed, line 174 does mention one-way PERMANOVA's but these are not listed in table S2. The axes of figure 2 are hard to read; can the font size be increased? Table S3 has a colour legend, it seems easier to read if you just write down the actual r values with asterisks for significance. Perhaps the editor can decide on this?
The r values shown in figure 3 and table s3 are significant, but only weak to moderate. I would reflect this in the text. Now, lines 262 to 264 could suggest to the reader that strong correlations have been found, which is not the case.
Discussion: Line 301: …., regardless of species (there was no interactive effect). Line 311: …showed a moderate correlation… I really like the discussion; perhaps the authors could also briefly touch upon the zoox densities found per se? The highest values, around 1 million zoox per cm2, are what we commonly find in healthy corals growing in aquaria (where nutrient levels are quite higher than in the field). I am unsure about common densities found in the field, but perhaps it would be interesting to briefly mention something about other field data from the literature. Are these densities in a typical range for the field?

Review form: Reviewer 2
Is the manuscript scientifically sound in its present form? Yes

Are the interpretations and conclusions justified by the results? No
Is the language acceptable? Yes

Do you have any ethical concerns with this paper? No
Have you any concerns about statistical analyses in this paper? Yes

Recommendation?
Major revision is needed (please make suggestions in comments)

Comments to the Author(s) See attached file (Appendix A).
Decision letter (RSOS-201835.R0) We hope you are keeping well at this difficult and unusual time. We continue to value your support of the journal in these challenging circumstances. If Royal Society Open Science can assist you at all, please don't hesitate to let us know at the email address below.

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Reviewer comments to Author:
Reviewer: 1 Comments to the Author(s) The authors have presented an insightful and well-written manuscript which is almost ready for publication. I only have a list of minor issues, which mostly concern the statistical part of the paper.

Methods:
Line 152: what is this conversion factor based on? I do not see sources. Is this based on the spectral light quality in situ?

Results:
Supplementary Table S1 lists no interactive effect of species and season on gene ratios. Thus, the authors can only resort to testing differences between seasons for both species combined (i.e. averaging the data from both species for each season). However, as shown in figure 1B, the authors have tested the means of the different seasons against each other per species. Splitting the data into both factors and doing pairwise comparisons like this can only be justified when the PERMANOVA first yields a significant interaction. I recommend testing the various seasons against one another without splitting the data into both species (i.e. performing a post-hoc test to follow up the significant main effect of season). Indeed, this is what the authors have done and described in lines 205 to 207. I would therefore change the pairwise comparisons in figure 1 to reflect these lines. Lines 194 to 198 should be removed as these suggest an interactive effect, which is not there. I would first report significant effects and then report the ratios which significantly differ, with species pooled. Supplementary table S2 should not list parts A and B, but should include C, where the species have been correctly pooled (and the rest of the table, of course). Interestingly, the authors did pool species for their correlations as described in lines 259 to 261. I agree with this approach, by the way. I hope the pairwise tests account for inflation of the familywise error (i.e. the p-values were corrected to compensate for multiple comparisons. Was this why you did parallel Monte Carlo tests)? I would make this issue clear in the M and M, because p values can be adjusted or a Bonferroni correction (with alpha / number of pairwise tests) can be done. In relation to this: Figure 1C is correctly done as there is a significant interactive effect for cell densities. Table S2 details pairwise comparisons for environmental variables (f to o), but I do not see a main PERMANOVA table with season as factor and a corresponding pseudo-F, which should be presented before performing pairwise (post-hoc) comparisons, correct? If so, table S1 should be expanded accordingly. Indeed, line 174 does mention one-way PERMANOVA's but these are not listed in table S2. The axes of figure 2 are hard to read; can the font size be increased? Table S3 has a colour legend, it seems easier to read if you just write down the actual r values with asterisks for significance. Perhaps the editor can decide on this?
The r values shown in figure 3 and table s3 are significant, but only weak to moderate. I would reflect this in the text. Now, lines 262 to 264 could suggest to the reader that strong correlations have been found, which is not the case.
Discussion: Line 301: …., regardless of species (there was no interactive effect). Line 311: …showed a moderate correlation… I really like the discussion; perhaps the authors could also briefly touch upon the zoox densities found per se? The highest values, around 1 million zoox per cm2, are what we commonly find in healthy corals growing in aquaria (where nutrient levels are quite higher than in the field). I am unsure about common densities found in the field, but perhaps it would be interesting to briefly mention something about other field data from the literature. Are these densities in a typical range for the field?
Reviewer: 2 Comments to the Author(s) See attached file.

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Recommendation? Accept as is
Comments to the Author(s) Thank you for your response. You have made good changes to your manuscript to address most of my concerns. While sequencing of qPCR amplicons was not pursued, I understand that it is often logistically difficult and/or impossible to do so for a project, especially if the experiments were completed multiple years ago. Even without any taxonomic data from the qPCR amplicons, the story presented in this manuscript is still clear and compelling. Nice work.

Decision letter (RSOS-201835.R1)
We hope you are keeping well at this difficult and unusual time. We continue to value your support of the journal in these challenging circumstances. If Royal Society Open Science can assist you at all, please don't hesitate to let us know at the email address below.

Dear Dr Tilstra,
It is a pleasure to accept your manuscript entitled "Relative abundance of nitrogen cycling microbes in coral holobionts reflects environmental nitrate availability" in its current form for publication in Royal Society Open Science. The comments of the reviewer(s) who reviewed your manuscript are included at the foot of this letter.
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Summary:
In this study, the authors seek to test the hypothesis that prokaryotic members of the coral holobiont regulate holobiont Nitrogen levels to maintain a stable symbiosis between the coral host and Symbiodinaceae and a healthy coral holobiont overall. Specifically, the authors sought to observe if the relative strength of denitrification vs. nitrogen fixation shifted in response to seasonal changes in Nitrogen availability (along with other parameters), and if this did or did not have an effect on Symbiodiniaceae cell counts in the coral holobiont. A coral reef in the Red Sea was surveyed seasonally for a variety of environmental parameters including DIN, DOC, DO, PAR, temperature, etc. Corals were also sampled at the same time scale, Symbiodiniaceae counts were taken, and qPCR was used to assess the relative ratio of nirS to nifH gene abundance as a proxy for the relative influence of denitrification and nitrogen-fixation. The effect of season on nirS:nifH ratios and Symbiodiniaceae cell densities as well as correlations between environmental parameters and these response variables were then tested.
Broadly, the authors found seasonal fluctuations in the relative nirS:nifH ratios and Symbiodinaceae cell counts. Correlations with environmental parameters demonstrated that nirS:nifH and Symbiodinaceae cell counts are positively correlated with environmental Nitrate availability. The authors conclude that a) seasonal fluctuations in nirS:nifH and Symbiodinaceae counts are driven primarily by Nitrate availability, b) increasing nirS:nifH in response to increasing Nitrate reflects beneficial behavior of prokaryotes in the coral holobiont, which could dampen fluctuations of Nitrogen in the coral relative to in the environment via changes in the relative strength of denitrification vs. nitrogen fixation, but c) this still was not enough to fully stabilize Symbiodinaceae populations.

Assessment:
This manuscript presents a fairly straightforward story on the role of nitrogen cycling prokaryotes in the coral holobiont. The order-of-magnitude changes in nirS:nifH fluctuations between seasons are compelling and the conclusion that this is driven by Nitrate availability makes sense. However, due to the nature of the data the paper can only make limited conclusions about what is happening within the coral holobiont. Specifically, a) qPCR only reflects gene copy number not necessarily rates of processes, b) no real conclusion can be drawn about how "beneficial" these changes may or may not be, and c) the actual availability of Nitrogen within the holobiont is never explicitly measured. Because of these gaps, I suggest the authors include additional data to strengthen their story.
Specifically, I think it would substantially bolster the paper to provide some information on which prokaryotes are responsible for the observed changes in nirS:nifH. The most straightforward way to do this would be to sequence the qPCR amplicons used in this paper. I recommend including this information in the next draft of the manuscript.
For the above reasons, I recommend major revisions to this paper prior to resubmission.

Line Comments:
52: Change from "including their" to "including by their" 57: Clarify to the reader that photosynthesis is done by Symbiodinaceae in the coral holobiont.

Appendix A
112: qPCR samples were run in technical replicates of 3. Were these averaged for each biological replicate prior to statistical analysis? Make this clear, because statistics should not be run on the technical replicates.
157-159: Where in the water column were the "sea water samples" taken?
172-173: Why were PERMANOVAs used? It is my understanding that two PERMANOVAs were run, one with nirS:nifH as the response variable and one with Symbiodiniaceae cell densities as the response variable (Table S1). In both cases, Season and Coral Species were the two predictor variables. If this is right then PERMANOVAs are being used on univariate data, which is an incorrect use of PERMANOVA since the response variable should be a distance matrix generated from multivariate data. Another type of model should be used (lm, glm, mixed mod, etc) that deals with univariate response variables (either normal or non-normal). The same holds true for all PERMANOVAs run on univariate environmental parameters. Additionally, individual identities of corals have been shown to influence microbiome community structure (along with other parameters), so any model that is run should use either a fixed or random effect to deal with the effect of "host ID"/"host genotype." 268: If both nirs:nifH and Symbiodinaceae cell densities are correlated with nitrate, why are they not be correlated with each other? Any ideas? There should be another panel in Figure 3 showing symb vs. nirs:nifH to visually show that they are not correlated. 289: Change "the here presented approach" to "this approach" 295-296: Some mention should be made of other processes in the N cycle that might be important in the coral holobiont.
323-325: The clause "this suggests that environmental N availability was closely linked with N availability within the coral holobiont in the present study as previously observed in ex situ studies" is crucial for your paper. N availability here is being measured in the water column, yet conclusions are being drawn about N availability in the coral holobiont. This implicitly assumes that N levels in water column reflect N levels in coral holobiont (at least before prokaryotic N cycling activities). You need to expand this clause to at least an additional sentence to really emphasize this to the reader. 338-340: "In this light, the observed increase in relative nirS to nifH gene abundance ratios with increasing N availability likely reflects a beneficial role of N cycling microbes in regulating N availability within the holobiont." This does not "likely" reflect anything. It is one possibility, but a more straightforward explanation is simply that changes in nifH:nirS simply reflect the changing availability of the substrates acted on by these processes in the coral holobiont. Change the above sentence to be more measured in its conclusions and read something more like "relative nirS to nifH gene abundance ratios shift in response to the availability of environmental N, which could prove beneficial to the coral holobiont by partly stabilizing N levels in the host relative to environmental fluctuations."

Reviewer: 1 Comments to the Author(s)
The authors have presented an insightful and well-written manuscript which is almost ready for publication. I only have a list of minor issues, which mostly concern the statistical part of the paper.
Our response: Thank you for the positive assessment of our manuscript.

Methods:
Line 152: what is this conversion factor based on? I do not see sources. Is this based on the spectral light quality in situ?
Our response: We have added the following information to the ms: "The conversion factor was obtained by inter-calibrating the lux readings (i.e., from the Onset HOBO Pendant) with data obtained from a parallel deployment of a PAR sensor (LI-COR LI-1500 quantum sensor) during 4 h of daylight. Both readings correlated (r 2 = 0.91) and the obtained conversion factor was 51.8." (see lines 153-156). Table S1 lists no interactive effect of species and season on gene ratios. Thus, the authors can only resort to testing differences between seasons for both species combined (i.e. averaging the data from both species for each season). However, as shown in figure 1B, the authors have tested the means of the different seasons against each other per species. Splitting the data into both factors and doing pairwise comparisons like this can only be justified when the PERMANOVA first yields a significant interaction. I recommend testing the various seasons against one another without splitting the data into both species (i.e. performing a post-hoc test to follow up the significant main effect of season). Indeed, this is what the authors have done and described in lines 205 to 207. I would therefore change the pairwise comparisons in figure 1 to reflect these lines.

Results: Supplementary
Our response: Thank you. We have adjusted the figure to show differences only per season. Accordingly, we changed the Results section to reflect these changes.
Lines 194 to 198 should be removed as these suggest an interactive effect, which is not there. I would first report significant effects and then report the ratios which significantly differ, with species pooled.
Our response: We argue that a short descriptive statement about the similar pattern of both species between seasons adds to the understanding of this figure. However, as the updated Figure 1 doesn't include differences between seasons within species anymore and based on the reviewers' comments concerning Table S2 we chose to delete lines 198-200 (from the old manuscript).
Supplementary table S2 should not list parts A and B, but should include C, where the species have been correctly pooled (and the rest of the table, of course). Interestingly, the authors did pool species for their correlations as described in lines 259 to 261. I agree with this approach, by the way. Table. C has been updated according to reviewer 2's comments.

Our response: Parts A and B have been deleted from the
I hope the pairwise tests account for inflation of the familywise error (i.e. the p-values were corrected to compensate for multiple comparisons. Was this why you did parallel Monte Carlo tests)? I would make this issue clear in the M and M, because p values can be adjusted or a Bonferroni correction (with alpha / number of pairwise tests) can be done. In relation to this: Figure 1C is correctly done as there is a significant interactive effect for cell densities.
Our response: Monte Carlo tests were indeed done in parallel to account for multiple comparisons. We've added this information to the manuscript, see lines 182-185.
Table S2 details pairwise comparisons for environmental variables (f to o), but I do not see a main PERMANOVA table with season as factor and a corresponding pseudo-F, which should be presented before performing pairwise (post-hoc) comparisons, correct? If so, table S1 should be expanded accordingly. Indeed, line 174 does mention one-way PERMANOVA's but these are not listed in table S2.
Our response: Table S1 has been expanded as suggested.
The axes of figure 2 are hard to read; can the font size be increased?
Our response: Figure 2 has been changed accordingly based on new statistics and suggestions from the reviewer. Table S3 has a colour legend, it seems easier to read if you just write down the actual r values with asterisks for significance. Perhaps the editor can decide on this?
Our response: We have updated the Table S3 as suggested.
The r values shown in figure 3 and table s3 are significant, but only weak to moderate. I would reflect this in the text. Now, lines 262 to 264 could suggest to the reader that strong correlations have been found, which is not the case.

Our response: Changed as suggested (lines 270 and 272).
Discussion: Line 301: …., regardless of species (there was no interactive effect).
I really like the discussion; perhaps the authors could also briefly touch upon the zoox densities found per se? The highest values, around 1 million zoox per cm2, are what we commonly find in healthy corals growing in aquaria (where nutrient levels are quite higher than in the field). I am unsure about common densities found in the field, but perhaps it would be interesting to briefly mention something about other field data from the literature. Are these densities in a typical range for the field?