Depth-resolved particle-associated microbial respiration in the northeast
Atlantic

Belcher, Anna; Iversen, Morten; Giering, Sarah; Riou, Virginie; Henson, Stephanie A.; Berline, Leo; Guilloux, Loic; Sanders, Richard

doi:https://doi.org/10.5194/bg-13-4927-2016

Articles | Volume 13, issue 17

https://doi.org/10.5194/bg-13-4927-2016

© Author(s) 2016. This work is distributed under
the Creative Commons Attribution 3.0 License.

https://doi.org/10.5194/bg-13-4927-2016

© Author(s) 2016. This work is distributed under
the Creative Commons Attribution 3.0 License.

Articles | Volume 13, issue 17

Research article

|

07 Sep 2016

Research article |

| 07 Sep 2016

Depth-resolved particle-associated microbial respiration in the northeast Atlantic

Anna Belcher, Morten Iversen, Sarah Giering, Virginie Riou, Stephanie A. Henson, Leo Berline, Loic Guilloux, and Richard Sanders

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Final revised paper (published on 07 Sep 2016)
Supplement to the final revised paper
Preprint (discussion started on 15 Apr 2016)
Supplement to the preprint

Interactive discussion

Status: closed

AC: Author comment | RC: Referee comment | SC: Short comment | EC: Editor comment

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RC1: 'Review of "Depth-resolved particle associated microbial respiration in the northeast Atlantic," by Belcher et al., 2015', Anonymous Referee #1, 10 May 2016
RC2: 'Referee #2 comments on "Depth-resolved particle associated microbial respiration in the northeast Atlantic" by Belcher et al.', Anonymous Referee #2, 16 May 2016
AC1: 'Author final response to reviewers', Anna Belcher, 24 Jun 2016
AC2: 'Revised manuscript as requested by Editor', Anna Belcher, 24 Jun 2016

Peer-review completion

AR: Author's response | RR: Referee report | ED: Editor decision

ED: Reconsider after major revisions (24 Jun 2016) by Koji Suzuki

AR by Anna Belcher on behalf of the Authors (24 Jun 2016) Author's response Manuscript

ED: Referee Nomination & Report Request started (28 Jun 2016) by Koji Suzuki

RR by Anonymous Referee #1 (30 Jun 2016)

Suggestions for revision or reasons for rejection

The authors have made extensive corrections based on the input of the two reviewers, resulting in an improved manuscript. However, I am still confused by the authors’ presentation of their hypothesis and the existing literature; the lack of clarity leaves the entire manuscript still very muddled. This is either due to a continued incorrect reading of the literature on the authors’ part, or a lack of clarity in the way they have presented it.

In the abstract: If, following from Giering et al., the authors are contending that two very different carbon budget regimes exist in the “upper” and “lower” mesopelagic ocean, this should be explicitly stated before anything else is presented. A great many studies have shown that respiration and other sinks can exceed carbon inputs in the mesopelagic, but there are very few that have shown the opposite… though this is not what the authors seem to be suggesting: “In particular, it has been suggested that organic-carbon supply exceeds respiration by free-living microbes and zooplankton in the upper mesopelagic.” If the authors mean that a very different situation exists in the upper mesopelagic than when considering the mesopelagic as a whole, then this contrast to the existing findings should be explicitly highlighted… and then the authors should very logically proceed to put their study in that context. Since this puts the authors “in the weeds” in terms of their study’s broader relevance, they should be very clear about the chain of logic. If this is correct, then the authors should define what they mean by the upper and lower mesopelagic.

Review document p. 42, line 17: I am not sure how the consistent standard errors with depth imply a lack of variability with depth in the factors driving C_spec. How does this work mathematically? Perhaps I am just missing the authors’ point here, but it seems to me one could obtain the same standard error despite large changes in the relative importance of various factors, so long as the increase in the strength of one was accompanied by a precisely complementary decrease in another.

Figure 9: I am not sure that completely removing the error bars was the right decision. Now, it appears the solubilization term has no uncertainty in it! I realize the authors have explained their intent in the caption, but the figure itself is now misleading. Since the authors are attempting to present real data and the results of a thought experiment in the same figure, this has to be very clear. Perhaps the label “Solubilzation” could be changed to “Solubilzation (hypothetical)” or something similar? Also, in (b) where are the error bars on the new zooplankton respiration data? Or the particle respiration data? The errors in these could be combined using statistical methods and presented somehow. Perhaps the entire panel in (b) needs to be marked off as hypothetical?

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RR by Anonymous Referee #2 (14 Jul 2016)

Suggestions for revision or reasons for rejection

SPECIFIC COMMENTS

Note: references made are to the revised manuscript.

Abstract, p. 1, line 19-20: from this sentence it seems that the study is designed to explore an excess of POC supply rather than a missing loss by respiration. The imbalance should be presented the other way around (i.e. the estimated respiration does not balance the observed flux attenuation of POC, suggesting a missing loss).

p. 2, line 7: please add Steinberg et al. [2008] to these references.

p. 2, line 9-11: same problem here, please rephrase the other way around.

p. 6, line 24: correct citation is Logan and Wilkinson [1990].

p. 6, line 25: again Fractal is not a shape it is a geometry! A spherical particle can have a fractal structure. However a sphere in the Fractal or Euclidean geometries has different structures (but a sphere with a fractal dimension of 3 is equivalent to an Euclidean sphere).

p. 7, line 22: replace µC individual-1 h-1 by µg C individual-1 h-1 if it is what was intended.

p. 8, line 28: please change "The low R2 shows that there is variability around this relationship, suggesting some heterogeneity in PA composition", to "The low R2 suggests that the influence of particle size on the sinking velocity is limited and that particle composition may exert a higher influence".

ADDITIONAL COMMENTS TO AUTHOR'S RESPONSES

GENERAL COMMENTS AND RECOMMENDATIONS

Note: references made are to the initial manuscript and first round of review

(3) "However, during the cruise a microbiology team performed parallel MSC deployments devoted to linking aggregate carbon content with microbial abundance."
How long will it take for these data to be produced? It might be worthy to wait for these and include it in the present manuscript.

SPECIFIC COMMENTS

p. 4, line 25: "Classifications were done manually by A. Belcher based on particle appearance. The morphologies were distinct allowing confident classification."
A manual classification should usually be avoided because highly subjective to the operator. You need to detail what criteria were used to decide how to sort the particles. I also find really surprising that natural particles had morphologies distinct enough so that they can be classified so easily by hand. Can you provide some kind of evidence that no mixed shape particles were observed?

p. 6, line 1: "... we observed particle formation after two days and aggregates increased in size during the incubation period."
Why then did you write in the initial manuscript p.10, line 21 "..., PAr POC contents could be reduced to 2 µg C mm-3 over 7 days (time incubated after first signs of aggregate formation)"? The first signs of aggregation were obtained after 2 or 7 days?!
"Additionally, a large number of the aggregates formed in the study of Iversen and Ploug (2010) fall in the range of sinking velocities that we measure on our roller tank formed aggregates (50-150 m d-1), suggesting that aggregation processes are not inhibited at this speed."
Again, there is absolutely no point in comparing the sinking velocities of particles made in different roller tank experiments from different primary particles and measured at different times. The only way to identify a potential effect of tank rotation speed on aggregation kinetic would be by comparing the time of apparition of the first aggregates from two roller tank experiments using the same material incubated at the same concentrations (preferably two identical phytoplankton cultures at the same stage), but using two different rotation speeds.

p. 7 lines 16-17: be careful with the use of "significant relationship" and "significant correlation". The low p-value indicates that the result of the statistic test is significant. However, the low R2 suggests an absence of correlation between PA sinking velocity and ESD. This is probably what you call "variability around the relationship".

p. 10, line 15: "... many studies still utilize roller tank to collect particles. We therefore thought that we could make additional useful comparisons of respiration rates".
Certainly not! Roller tank experiment are only designed to form particles artificially, not to collect them. The way you justify why you conducted this roller tank experiment is still not satisfying. Why did you want to compare respiration rates of roller-tank made particles with natural particles? (especially because you noted that these particles were not sampled at the same depth).
"...in an attempt to assess the aggregation potential in the most productive water strata"
How do you assess the 'aggregation potential'? Roller tank experiments are unfortunately useless at such a task, because they cannot be used for quantitative studies [Jackson, 1994].
Based on this, I am still not convinced of the interest of including this roller tank experiment in the manuscript and will let the editor decides whether it has to be removed or not.

REFERENCES CITED

Jackson, G. A. (1994), Particle trajectories in a rotating cylinder: implications for aggregation incubations, Deep-Sea Research Part I: Oceanographic Research Papers, 41(3), 429--437, doi:10.1016/0967-0637(94)90089-2.

Logan, B. E., and D. B. Wilkinson (1990), Fractal geometry of marine snow and other biological aggregates, Limnology and Oceanography, 35(1), 130-136, doi:10.4319/lo.1990.35.1.0130

Steinberg, D. K., B. A. V. Mooy, K. O. Buesseler, P. W. Boyd, T. Kobari, and D. M. Karl (2008), Bacterial vs. zooplankton control of sinking particle flux in the ocean's twilight zone, Limnology and Oceanography, 53(4), 1327.

Referee Report: PDF

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ED: Reconsider after major revisions (14 Jul 2016) by Koji Suzuki

AR by Anna Belcher on behalf of the Authors (28 Jul 2016) Author's response Manuscript

ED: Referee Nomination & Report Request started (01 Aug 2016) by Koji Suzuki

RR by Anonymous Referee #1 (09 Aug 2016)

Suggestions for revision or reasons for rejection

The authors' revisions during the second round of review have improved the manuscript dramatically. Their message is clear, and their presentation now does a fantastic dataset adequate justice. I have only a two very minor (easily fixable) comments pertaining to the way the authors have phrased their statements of the carbon mass imbalance in response to the second reviewer's comments.

p. 9: Currently: "In particular, it has been suggested that respiration by free-living microbes and zooplankton in the upper mesopelagic are too low to balance observed flux attenuation of POC within this layer." As in my comment below, this phrasing doesn't make sense mathematically. Respiration and flux attenuation are both loss processes (sink terms), so there is no source here that would provide any sort of balance. I understand what the authors are attempting to say, but a small change should be made to make this correct, in a mass balance sense. Could try "... upper mesopelagic is too low to explain observed flux attenuation of POC within this layer." or " ... upper mesopelagic is too low to balance observed inputs of POC within this layer." Both would be correct.

p. 10: Currently: "Ultimately carbon is lost from the organic carbon pool as carbon via respiration, and hence, in theory at steady state, community respiration should be balanced by the loss (attenuation) of POC (Burd et al., 2010)." I fully understand what the authors are attempting to express here, but it does not make sense mathematically as currently stated. In the mass balance, community respiration isn't balanced by the loss of POC because community respiration is *itself* the loss process. The way it is currently phrased, there is no balancing input term! Instead, how about "... respiration should be balanced by the supply of POC" or something similar. The plain-language description should parallel a written equation. (The authors phrase the situation correctly in the sentence immediately following.)

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ED: Publish subject to minor revisions (Editor review) (21 Aug 2016) by Koji Suzuki

Dear Authors,

One of the former referees and I are very pleased to find that your manuscript has been improved significantly. However, there are still a few minor comments from the expert (see below). So we would appreciate it very much if you could make a further revised manuscript.

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

Kind regards,

Koji Suzuki
Editor

---

The authors' revisions during the second round of review have improved the manuscript dramatically. Their message is clear, and their presentation now does a fantastic dataset adequate justice. I have only a two very minor (easily fixable) comments pertaining to the way the authors have phrased their statements of the carbon mass imbalance in response to the second reviewer's comments.

p. 9: Currently: "In particular, it has been suggested that respiration by free-living microbes and zooplankton in the upper mesopelagic are too low to balance observed flux attenuation of POC within this layer." As in my comment below, this phrasing doesn't make sense mathematically. Respiration and flux attenuation are both loss processes (sink terms), so there is no source here that would provide any sort of balance. I understand what the authors are attempting to say, but a small change should be made to make this correct, in a mass balance sense. Could try "... upper mesopelagic is too low to explain observed flux attenuation of POC within this layer." or " ... upper mesopelagic is too low to balance observed inputs of POC within this layer." Both would be correct.

p. 10: Currently: "Ultimately carbon is lost from the organic carbon pool as carbon via respiration, and hence, in theory at steady state, community respiration should be balanced by the loss (attenuation) of POC (Burd et al., 2010)." I fully understand what the authors are attempting to express here, but it does not make sense mathematically as currently stated. In the mass balance, community respiration isn't balanced by the loss of POC because community respiration is *itself* the loss process. The way it is currently phrased, there is no balancing input term! Instead, how about "... respiration should be balanced by the supply of POC" or something similar. The plain-language description should parallel a written equation. (The authors phrase the situation correctly in the sentence immediately following.)

Please find below the report of the second reviewer:

�GENERAL COMMENTS AND RECOMMENDATIONS

The authors have thoroughly addressed all comments and recommendations
made in the 2nd round of review. The manuscript has been considerably
improved since the first submission and significantly gained in clarity. In
particular, the objectives developed in the introduction, the analyses
conducted and the conclusions are now in-line and flow logically along the
different sections. By removing all elements related to the roller tank
experiment, the authors strengthened the manuscript and enhanced its
coherence.
I can now strongly recommend this manuscript for publication in
Biogeosciences and salute the authors for their rigorous work. Below are
some minor technical corrections to be addressed at the authors'
convenience.

TECHNICAL CORRECTIONS

Note: references made are to the revised manuscript.
p. 2, line 5: add Fran�ois et al. [2002]
p. 3, line 5: change "estimated" to "estimate".
p. 4, line 13: "... at which depth the bottles were closed,..." This sentence
sounds incorrect. Maybe try to rephrase it.
p. 5, line 1: "... and F0 is flux at the reference depth...". Add "the" between "is"
and "flux".
p. 5, line 6: change "aggregations" to "aggregates" if it was the word intended.
p. 5, line 9: "Conversions from PA volume...". It seems like a "to" should follow
the "from". Check the sentence.
p. 5, lines 26-27: "PA volumes were calculated from...". This sentence does
not read nicely, try to rephrase it.
p. 5, line 30: remove the parentheses enclosing "50-200 ?m".
p. 6, line 20: to be consistent you should give the form of the power-law
relationship as you did for the exponential fit later in the sentence.
p. 6, line 31: "We conduct...". The remaining of the paragraph is at the past
tense. I noticed a large number of inconsistencies in the use of present and
past tense in the manuscript. Please check this.
p. 7, line 24: change "(Ikeda, 1985)" to "Ikeda (1985)".
p. 8, line 2: change "chlorophyll-a" to "chlorophyll a".
p. 8, lines 15 to 18: you use the same kind of explanations for the lack and
increase of FP, maybe you could try to combine them.
p. 8, line 25: "... showing consistency in the composition of the bulk of sinking
PA." This is very hard to affirm this considering the multiple controls on
aggregate sinking velocity (e.g. composition, structure, size, shape).
p. 8, line 26: again I disagree: there is no significant correlation between size
and sinking velocity! And your last sentence (lines 28-29) contradicts this
statement. Please fix this.
p. 9, line 2: "Consistent with other studies...". Please cite them.
p. 10, lines 8-9: "This may reflect the heterogeneity of aggregate composition
in terms of the availability of labile carbon...". Please rephrase this sentence.
p. 10, line 25: "quite constant" does not mean anything. Maybe you can
replace it by "small variations"?
p. 12, line 31: "... with an oversupply of POC in the upper mesopelagic and an
undersupply in the lower mesopelagic". The "oversupply" and "undersupply"
refer to bacterial demand, you should mention it.

REFERENCES CITED

Fran�ois, R., S. Honjo, P. Krishfield, and S. Manganini (2002), Factors
controlling the flux of organic carbon to the bathypelagic zone of the ocean,
Global Biogeochemical Cycles, 16(4), doi:10.1029/2001gb001722.

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AR by Svenja Lange on behalf of the Authors (22 Aug 2016) Author's response Manuscript

ED: Publish subject to technical corrections (26 Aug 2016) by Koji Suzuki

AR by Anna Belcher on behalf of the Authors (26 Aug 2016) Author's response Manuscript

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Short summary

We address the imbalance between the supply and loss of organic carbon to the upper layer of the ocean by measuring a previously poorly quantified term: particle-associated microbial respiration of in situ particles. We find rates that are too low to account for the missing sink of carbon and suggest instead that zooplankton drive the transformation of large fast-sinking particles into slow-sinking and suspended particles. This apparent loss may help explain imbalances in the carbon budget.