Dear Dr. Agustí,

Thank you very much for responding the reviewers' comments carefully. We would appreciate it very much if you could submit a revised version of your manuscript to us. Once we receive the paper from you, I am asking the referees again for further evaluation.

Again thank you for your nice efforts to improve the manuscript.

Kind regards,

Koji Suzuki
Associate Editor

Dear Dr. Agustí,

We have received two reviews on your revised manuscript from the previous referees. Although one reviewer was pleased to find some improvement from the former version, another referee still had serious concerns, especially in the experimental setup. Also, the latter reviewer considered that your conclusions were not fully supported by the results obtained from this study (see the details below).

Therefore, if you strongly consider that you can logically dismiss the concerns mainly raised by the second reviewer, please make a further revised manuscript and submit it to us with your point-by-point responses to the reviewers’ comments. We will send your further revised manuscript to another expert for further review.

Thank you very much again for your time and nice efforts to improve the manuscript.

Kind regards,

Koji Suzuki
Associate Editor

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Reviewer #1

Revised MS has been improved to describe the Author’s logic more clearly along the line of (1) nutrient depletion leads unhealthy status of diatom --> (2) unhealthy/senescent diatom sinks down faster than healthy diatom --> (3) diatoms reaching the aphotic zone die and lyse soon --> (4) downward export of unhealthy/senescent diatom increase the progression of the surface pCO2 unsaturation. Results from the experiments fully support (2) and (3), but not (1), even though many previous studies suggest it. I would like to request Authors (i) to state insignificant correlation between nutrient concentrations and %living biomass in the photic zone, and, (ii) if possible, to cite the previous studies on the mechanisms driving diatom senescence other than nutrient depletion. My other concern is about (4), as rapid lysis of senescent diatoms (3) might result in supply of suspended/dissolved organic carbon and their remineralization within the subsurface waters which reduces air sea disequilibrium in the surface through processes such as upwelling, mixing and vertical diffusion (Bates and Mathis, 2009). I suggest Authors (iii) to explain the contradicting effects of (2) and (3) for the surface pCO2. There are many errors in writing. I recommend (iv) to ask an English proofreading service before re-submission. I hope my comments would help Authors to enhance the value of their findings.

Specific comments
p. 4, l. 26: Write the station ID (#3?) whose sample was used in the sinking experiment.

p. 5, l. 7: NO3 should be NO3 + NO2.

p. 6, l. 2 – 4: “At station #4, the community sampled was more diverse at the aphotic than at the photic layer (Fig. 4) indicating high sinking despite the low biomass.” Why does high sinking rate contribute to higher diversity in the aphotic zone than that in the photic zone?

p. 6, l. 17 – 16: “Initially, only 6.7 % of the cells of the Fragilariopsis sp. and Thalaisiosira sp. colonies dominating the community tested were dead.” It seems there is no stations where these two species were dominant in Fig. 4. Again, at which station was the sinking experiment conducted?

p. 6, l. 29 – 30: “6.3 days for the largest Thalaisiosira sp. cells” “6.3 days” would be “5.3 days”.

p. 7, l. 18: “..., although diatom sinking was still low. “ Was it confirmed at this station?

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Reviewer #2

Why I agree that bottle net, is a very exciting and original tool, the results here are still too poor to be used alone or to state that silicon is the trigger of the bloom senescence and sinking.
I disagree with the authors when they state that they include a sufficient amount of data to strengthen this paper. To my point of view, the paper rely too much on two experiments that were not robust enough to conclude anything, especially for the one where we could find some opposite results in the literature (which is not discussed at all). At the minimum this paper should discuss the problem with the experimental set up.
Diatom survival to darkness:
I am still not convince by this experiment that aim at measuring the survival of diatom in the dark…
First, if I understood correctly it has only be done once and only at St 3.
Second, I am not sure that the experimental protocol was sufficiently robust to conclude anything from it.
What was the health status of the cells at the start of the experiment? How the same cells would survive in the same conditions but with light? What was the cell concentration in the experiment? The experiment was done at 4°C what was the in situ temperature? You started with a very limiting silicate concentration, so how could you state that darkness is responsible for the death of the cells? Multiple nutrient stress in the batch may have be the trigger for the diatom death…
Third, the results are not at all compared to other study where the authors stated something totally different from a more robust experimental set up:
Why are these results so different from the one by Smayda and Mitchell-Innes 1974 showing survival of diatoms for 90 days in the dark?
And by the study by Lewis et al. 1999 where some diatoms even survive up to 112 month?
The authors already observed some living diatoms really deep in the water column during the Malaspina expedition, so why would it be different in arctic?

Diatom sinking triggered by the health status of the cells:
As there was more than one sampling, it could have been nice at least to have the composition of the sample at the different time. However, the authors need to be a lot more careful in their discussion as they only tested one community once. While the idea behind is interesting, it is not enough experiment to conclude.

P5
Line 28: Fig. 2 should be Fig. 3
Line 36: Navicula does not dominate the Barent Sea the composition look much alike St3
P6
Line 20: what was the main species after one hour?
Line 30 : how to concile with result showing some Thalassiosira starting back in culture after 70 days in the dark?

P7
Line 29: “depleted silicic acid silicic acid limits diatom Si uptake to such a degree that growth must slow, Krause et al” please add a coma or a colon for clarity
Line 30: but you show that they stay alive only shortly after they leave the photic zone
Line 31-33: I don’t understand your sentence here that state that diatom mortality is triggered by Si limitation, especially as what you explained in the next paragraph is more like Si limitation trigger the loss of buoyancy and the darkness trigger the death of the cell, no?
P8
Line 10: aphotic instead of photic?

Dear Dr. Agustí,

We received new comments on your revised manuscript from another expert (see below). Although the new reviewer was interested in your results, the expert has also a number of concerns about your manuscript. For example, you found differences in diatom assemblages between the euphotic and aphotic layers, but the referee considered that the number of the data was insufficient to get your conclusions. Please confirm all comments from the reviewer and make a further revised paper with point-by-point responses.

Thank you again for your nice effort to improve the manuscript.

Best regards,

Koji Suzuki
Associate Editor

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The article studies the impact of life stage of diatoms on their vertical export in the Svalbard area. The article would confirm the hypothesis that unhealthy diatoms are sinking whereas the healthy ones maintain better buoyancy and rather stay at surface.

I quite enjoyed the reading and I found it very instructive.

First, the topic is highly strategic and interesting. Diatoms dominate the primary production in this very productive region. However, very few (or no?) studies have in situ measurements. The hypothesis that senescent diatoms sink is often use without proper in situ proof. For these reasons, I think this article could potentially provide a valuable contribution.

However, I could just agree with the other reviewers. I have concerns about the significativity of the results which are based on a very limited dataset. Yes, the authors found significative differences between photic and aphotic communities but still, this is a very weak. I acknowledge that the authors have done a great effort to re-frame their results during the review process and that there is not much more information to extract from the data set. I recommend say ‘moderate’ revisions to address remaining issues.

About the rate of mortality, I agree with most of the authors answer to reviewer #2. But I deeply encourage authors to be more specific. For example, it was not clear, before I read the answer to reviewer #2 the subtilty in the terminology of “survival”. Please clarify that you only consider vegetative cells here. Because this is clear there is survival of (resting) cells in the dark for a long period of time.

Perhaps it could serve also in the discussion to understand that your approach is different from other studies. I have to admit I had exactly the same reaction than reviewer #2 during my first read of the revised manuscript (first appeared contradictory with the literature I know)

I was also surprised some major references were not listed in your study. As global critic, this article still lacks of contextualization. Some articles (see below in gray) that I found related (you are not obliged to cite those but it could help you to improve the discussion).

See for example:

Kvernvik et al. 2019, https://doi.org/10.1111/jpy.12750. They say for example: “Our results suggest that some Arctic autotrophs maintain fully functional photosystem II and downstream electron acceptors during the polar night… This could allow Arctic microalgae to endure the polar night without the formation of dormant stages, enabling them to recover and take advantage of light immediately upon the suns return during the winter–spring transition.”. I am really surprised the authors did not take more precaution while discussing this still debated topic.

In Berge et al. 2015:
“Many Arctic phototrophic plankters are able to persist during unfavorable conditions as resting stages such as spores or cysts (Garrison, 1984; Smetacek, 1985; Krempand Anderson, 2000), and diatoms are known for their potential to survive long periods of darkness (Antia and Cheng, 1970; Smayda and Mitchell-Innes, 1974; Palmisano and Sullivan, 1982; Sakshaug et al., 2009; Quillfeldt et al., 2009). The survival strategies of the various plastidic flagellates of Arctic waters throughout the dark period, however, are largely unknown.”

Lacour et al. (2019) also suggest the opposite (https://link.springer.com/article/10.1007%2Fs00300-019-02507-2))
“Chaetoceros neogracilis was not able to grow in the dark but cell
biovolume remained constant after 1 month in darkness. Rapid resumption of photosynthesis and growth recovery was also found when the cells were transferred back to light at four different light levels ranging from 5 to 154 μmol photon m−2 s−1. This demonstrates the remarkable ability of this species to re-initiate growth over a wide range of irradiances even after a prolonged period in the dark with no apparent lag
period or impact on survival.”

As well as the extensive synthesis by Wulf et al. 2008 (https://www.tandfonline.com/doi/abs/10.1080/0269249X.2008.9705774)
“Based on the rapid increase in Fv/Fm we safely draw the conclusion that although the
cells probably were physiologically resting in the dark they were not forming resting stages
such as spores or cysts. Physiologically resting cells are morphologically similar to the
vegetative cells, but are physiologically dormant and can be induced when cells are transferred to cold and dark conditions (Anderson 1975a). Like in our study, these cells have condensed protoplasts which are transformed back to the former state (within hours) upon re-exposure”

________________________________________________________________


How the authors can be 100% confident that their unique culture experiment was reliable?
Did something else than darkness could have killed the algae (i.e. contamination?) ?
Could you discuss that ?

Also, there is many syntax, grammar and terminology issues in the text (lot of them were introduced during the revision process, that is a pity). I recommend to carefully correct the text because it makes the understanding sometimes difficult (I had to re-read many sentences many times). I have tried to list them in the specific comments but it became quickly overwhelming.

I encourage the authors to continue their efforts.

Specific comments:

PAGE9 (abstract).
L.23: specify phytoplankton bloom, it could be sea ice algae. Or if no distinction, just microalgae.
L.26: regional = specify Svalbard or Northwest Barents Sea
L.27-28: very awkward sentence. Change “occurrent with” something like “together with”.
L.29: SE= Standard Error ? I don’t think you could use undefined abbreviation in the abstract. Need confirmation from editor.

PAGE11 (2.1)
L.23: you canno’t say MLD is an indicator of stability. Stability is usually related to stratification. Stratification is basically the density gradient which you don’t measure here. MLD is an indicator of mixing, this is it. People know what is MLD (or UPM), I suggest you just erase “an index of the stability of the water column” and also later in the text.

PAGE12 (2.3)
L.32 Move “expected” before “mortality”.
L.35: I can understand but this is not well written. Perhaps change “, this simulated” par “simulating” ? or “which simulated” ?

PAGE13 (3)
Please be consistent and use either r or R2 throughout the manuscript.

PAGE14
L.10: N or n ?
L.13: “from station 6 to station8”
L.14: a E is missing in the verb were. Change “these wre also the areas with” by something like “and where”

L.31-32: this is interpretation, should be moved in discussion.

PAGE 15, LINE 5 and PAGE 16 LINE 7: please do not use the term trend in this context. This is not appropriate, please re-word.

PAGE16
Line 23: amoung out ??? amoung OUR ?
Line 35-37: weird wording, had to re-read several times. I guess you wanted to say sedimentation is enhanced BY higher quotas for polar diatoms. Please re-word.

It is a great pleasure now to accept your manuscript for publication in Biogeosciences. Thank you very much for responding to the reviewer's comments carefully. Although the observation data for supporting the hypothesis that dead diatom cells sink faster than vegetative cells is still limited even in this study, I believe such data would be crucial in the future for considering the fates of carbon and other elements derived from diatoms in more depth.

Before it is published, please consider technical suggestions from the referee and me.

Thank you again for your nice efforts to improve the manuscript.

Sincerely,

Koji Suzuki
Associate Editor

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Referee’s comments:

I accept this article.
I would just recommend to delete the following sentence:

"We cannot rule out that contamination from the vessel during experimental preparations may affected mortality rates in the incubations."

It is already stated in the discussion paper so the reader can refer to it.
It is fair enough to me, there is no need to state in the main text.

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Editor’s comments:

P1, L35: faster “than” living cells
P4, L17: Not Syto 9, but SYTO 9.
P5, L26: two-tailed test
P6, L3 and hereafter: “sp.”. Were these truly single species? If not, please use “spp.” Also please check this issue throughout the manuscript.
P7, L16: Not diatoms cells, but diatom cells.
P7, L32: (Lacour et al., 2019)
P8, L1: longer photoperiods than in winter when surviving cells are …
P8, L24: Krause et al., 2018
P8, L34; Rey, 2012
P9, L23: Wassmann et al., 2006;
P9, L26: Bates et al., 2009;
P10, L7 and hereafter: 543, 89–126, 2016. Please use en dash (–) for the page range. Also check this issue in other references carefully.
P14, L15; P14, L30; P14, L31: P < 0.05
P14, L28: (a) large celled Thalassiosira spp., …, (c) Thalassiosira spp., and (d) pennate diatoms (?)