A meta-analysis of microcosm experiments shows that dimethyl sulfide (DMS) production in polar waters is insensitive to ocean acidification

Hopkins, Frances E.; Nightingale, Philip D.; Stephens, John A.; Moore, C. Mark; Richier, Sophie; Cripps, Gemma L.; Archer, Stephen D.

doi:https://doi.org/10.5194/bg-17-163-2020

Articles | Volume 17, issue 1

https://doi.org/10.5194/bg-17-163-2020

© Author(s) 2020. This work is distributed under
the Creative Commons Attribution 4.0 License.

https://doi.org/10.5194/bg-17-163-2020

© Author(s) 2020. This work is distributed under
the Creative Commons Attribution 4.0 License.

Articles | Volume 17, issue 1

Research article

|

16 Jan 2020

Research article |

| 16 Jan 2020

A meta-analysis of microcosm experiments shows that dimethyl sulfide (DMS) production in polar waters is insensitive to ocean acidification

Frances E. Hopkins, Philip D. Nightingale, John A. Stephens, C. Mark Moore, Sophie Richier, Gemma L. Cripps, and Stephen D. Archer

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Final revised paper (published on 16 Jan 2020)
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Preprint (discussion started on 19 Feb 2018)
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Status: closed

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

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RC1: 'Review of Hopkins et al', Anonymous Referee #1, 20 Mar 2018
- AC1: 'Final author comments', Frances Hopkins, 21 Jun 2018
RC2: 'Review on ‘Dimethylsulfide (DMS) production in polar oceans may be resilient to ocean acidification’ by Hopkins et al.', Anonymous Referee #2, 12 Apr 2018
- AC2: 'Final author comments', Frances Hopkins, 21 Jun 2018
AC3: 'Comment from lead author', Frances Hopkins, 28 Feb 2019

Peer-review completion

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

ED: Reconsider after major revisions (18 Jul 2018) by Gerhard Herndl

AR by Frances Hopkins on behalf of the Authors (19 Jul 2018) Manuscript

ED: Referee Nomination & Report Request started (12 Aug 2018) by Gerhard Herndl

RR by Anonymous Referee #2 (26 Aug 2018)

Suggestions for revision or reasons for rejection

After reading manuscript and responses of the authors, I am disappointed with the revision. While the authors implemented many comments, most of my substantial criticism has either been rejected (e.g. 2.6, 2.16, 2.23, 2.24, 2.25, 2.30) or not accounted for appropriately, i.e. by just deleting part of the manuscript instead of discussing potential inconsistencies (e.g. 2.38). It seems to me that any criticism that questions the general interpretation of the dataset has not been included. Under these circumstances, I am not willing to provide a point by point reply to the response, but just highlight the most important points.

Most importantly, I still not agree with using the nominal carbonate chemistry levels instead of the actual data. As already described in the first round of reviews, control and OA treatments diverge strongly in some of the experiments. As can be seen in table SI1, measured pCO2 levels varied strongly from the nominal values at all time points, and this discrepancy seems to be larger in the polar compared to the temperate experiments. Already at t0, actual values at 100 and 1400 µatm in both polar areas were in most cases several hundred µatm lower than assigned, i.e. about 20-40% lower. This trend is even more pronounced at T2, where measured pCO2 values are as low as 362 µatm in the 750 µatm, 421 µatm at the 1000 µatm, and 767 µatm in the 1400 µatm treatment. These pCO2 levels in the OA treatments significantly overlapped with control conditions. Thus, the presented carbonate chemistry data clearly does not meet the quality requirements of our scientific community, and therefore the nominal levels cannot be used for data analysis.

Similarly, I still disagree with the statement that “a narrow range of values for all carbonate parameters was observed in the NW European shelf waters relative to the less well-buffered Arctic and Southern Ocean waters“ (new L 490-492). As can be clearly seen in Figure 9, CT/AT ratios (which the authors use as a proxy for buffer capacity) were actually higher in the SO compared to the NW European shelf waters which had the lowest median. The “much larger” variability in polar waters (response letter 2.30) is in fact only observed for the Arctic. These facts clearly contradict the authors conclusion that “that populations from higher latitude, less well-buffered waters, already possess a certain degree of acclimative tolerance to variations in carbonate chemistry environment” (new L 646-648).

Lastly, I still find the question of coastal/open ocean vs. polar/temperate differences not resolved. The authors wrote in the first version of the manuscript: “We provide further evidence that, in contrast to temperate communities (Hopkins and Archer 2014), polar communities we sampled were relatively insensitive to variations in carbonate chemistry (Davidson et al. 2016; Richier et al. under review), manifested here as a minimal effect on net DMS production. Our findings contrast with two previous studies performed in coastal Arctic waters (Archer et al. 2013, Hussherr et al. 2017) which showed significant decreases in DMS in response to OA.” After my comment that this contradicts their hypothesis of generally higher sensitivity of polar compared to temperate communities, the authors just omitted the description of the two cited studies as being “coastal” (response letter 2.38), instead of adapting their discussion to the fact these two coastal studies with higher natural carbonate chemistry variability contradict the hypothesis brought forward in this study. I the response letter, the authors furthermore argue that “The carbonate chemistry/pH variability may be as large in the open waters of the polar oceans as in coastal sea ice waters” (1.11) and they cite two studies to support this statement. It is a well-known and widely accepted fact, however, that coastal sites experience larger environmental variability that oceanic ones. For example, the study by Thoisen et al. (2015) that I referred to already in the first review, showed report a seasonal pH gradient as large as 0.8 units (7.5 -8.3) for a costal Arctic site. In conclusion, I am still convinced that the CO2 sensitivity observed in two previous coastal studies contradicts the hypothesis of this study. The attempt to just ignore instead of discuss this apparent contradiction is, in my view, not an acceptable scientific practise.

Please also note that in my view, papers should be understandable and convincing by themselves. So while I did read Richier et al. (2018), I am providing my views on the current manuscript only.

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RR by Anonymous Referee #3 (17 Sep 2018)

Suggestions for revision or reasons for rejection

General Comments
The paper describes a series of high pCO2 incubation experiments performed on three cruises in temperate, Arctic and Southern Ocean waters during the summer period in each location. Studied in the incubations are the changes in DMS and DMSP over the short term (hours to days), and the changes in production rates of these compounds. The manuscript is clear and well written, and highlights the regional differences in the response to elevated pCO2, and attributes the differences to the variability in the carbonate system. Given that two of the environments studied were in polar regions, discussion of the effect of sea ice on the carbonate chemistry and the existing response of the phytoplankton community to extreme environments was lacking within the manuscript, particularly a mention of the pH changes experienced by cells while living within the sea ice.
A number of technical and specific comments arose on reading of the manuscript, and I recommend publication if these can be addressed.
Check pCO2 is in italics, as there were instances where it was not.

Specific comments
L28. ‘This implies that…’ The previous sentence did not suggest this implication, so needs rewording. It seems like a sentence is missing here, which actually describes your findings, and is followed by the implication.
L71 Please highlight that the 3.4 Tg S is from the whole southern ocean, as calculated by JT16.
L88. Is there a concurrent predicted decrease in the southern polar region pH as well?
L96. During the introduction there is very little mention of DMSP, other than it is the precursor for DMS. Given that DMSP is one of your measured parameters in the experiments this requires further elaboration in the introduction, in particular the changes in DMSP as identified from the existing mesocosm experiments. This is important given that DMSP showed increases during the Arctic mesocosm.
L100-117. This section on mesocosms is interesting, but slightly irrelevant to the paper as a whole given that your studies are microcosm incubations. As the introduction is already very long, this section could be shortened to one or two sentences describing previous OA responses.

L114 High cost is also a significant factor in why mesocosm experiments are so limited!
L120. Please clarify that the temperate experiments shown here are in addition to those in Hopkins and Archer 2014; ie this manuscript includes four previously unpublished temperate experiments, as well as those previously published.
L136, remove additional comma before reference.
L142 What are the main differences in the environment between temperate and polar environments? You have not mentioned the distinct seasonal cycle of sea ice formation and retreat, different at both poles, which will likely also alter the carbonate chemistry. Does the acclimation of polar phytoplankton to the physiological stress of survival through the polar winter give them an added advantage when it comes to acclimating to OA? Is DMSP produced by polar phytoplankton (i.e. osmoregulation during periods of extreme salinity shift) for a different reason than temperate phytoplankton?
L190 pCO2
L222. In the southern ocean, was this acidification fixing method used for the DMSP samples, given previous issues highlighted by del Valle et al 2011 in samples containing Phaeocystis antarctica?
L253 spaces missing between mass 63 etc.
L281 composition used twice in the sentence.
L317. Please state the station where 1.5 µg L-1 was identified, as you have for the minimum.
L318.’reflected in’. Please reword, firstly as reflected implies light reflectance (given the topic of irradiance), and secondly it reads oddly with two instances of ‘in’.
L320 – 328. Use of nM when the following paragraph uses nmol L-1
L327. Could not understand the significance of the superscript 1, is it a typo?
L480. Should P be lower case?
L485. In this section I would like to see more discussion of sea ice and the extreme environment is imposes on the cells, which could account for some of their resilience to change. Many polar phytoplankton survive the extreme cold of the polar winter by living within the sea ice itself, in an extremely changeable habitat, and these cells seed the surface waters in summer time on melting of the sea ice. Cells are regularly exposed to hypersaline and highly nutrient variable environments, at temperatures below freezing, and in highly elevated pH environments (Thomas and Dieckmann 2002, Rysgaard et al 2012). Although your experiments were not associated directly with the polar sea ice and occurred during summer, the influence of the ice on the phytoplankton population will be dependent on the seed populations, and allow for greater tolerance of the incubation perturbation than in temperate communities. In the seasonal cycle of the Antarctic, the behaviour of the summer phytoplankton community development is dependent on the conditions experienced the previous winter (Venables et al 2013).
L523. P in italics
L561. Hopkins reference is 2010b, but only 1 Hopkins 2010 ref is present.
L609 italic p
L626, commas missing from references.

Referee Report: PDF

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ED: Reconsider after major revisions (07 Oct 2018) by Gerhard Herndl

AR by Frances Hopkins on behalf of the Authors (26 Sep 2019) Author's response Manuscript

ED: Referee Nomination & Report Request started (01 Oct 2019) by Katja Fennel

RR by Anonymous Referee #1 (17 Nov 2019)

Suggestions for revision or reasons for rejection

General comments
The paper describes the results of microcosm experiments examining the response of DMS and DMSP concentration, synthesis & production rates to acidification in Southern Ocean & Arctic waters, and compares them with previously published results from the NW European shelves. The primary results are the absence of an effect of high CO2 on DMS/DMSP in polar waters, and the contrasting significant effect of high CO2 in decreasing DMSP concentration/DMSP production & increasing DMS production in temperate waters. The authors relate the difference in regional DMS response to variability of the carbonate system of each region; other factors (phytoplankton community, nutrients etc) are rejected due to the absence of significant relationships. The paper makes some interesting points regarding regional variation in response to acidification, which should be considered in models.

I have two “medium” concerns with paper, the first being that the DMSP response to High CO2 is a little overstated; a significant DMSP response to High CO2 is limited to the first 48 hours in the polar experiments, after which there is no significant difference from the control. My other concern is that the interpretation, and proof of their hypothesis, rests on differences in regional variability of pH & the carbonate system, yet the data presented to support this are somewhat limited. I appreciate there are limited pH datasets available, but the data discussed are primarily large-scale spatial variability, and not the temporal variability that the phytoplankton experience.

Specific comments
Title doesn’t scan as written (“IS insensitive”) and is a little confusing with reference to the polar results, & then then the metanalysis of polar AND temperate results. A better title might be:
“DMS sensitivity to ocean acidification as determined in a meta-analysis of temperate to polar microcosm experiments”
Or, to highlight the polar results:
“A metanalysis of microcosm experiments shows that DMS production in polar waters is insensitive to ocean acidification”

Abstract
Line 26 “resulting in an INCREASE in DMS emissions to the atmosphere…..”

Discussion
Line 443-445; The text implies there is a significant positive effect on DMSP of high CO2 at the 2nd time point, but this does seem apparent in Fig. 7D
Line 450 “This data suggests that DMSP concentrations in polar waters may be upregulated…” again this is only for the first 48 hours; Fig 7D doesn’t show a significant mean effect at 96 hours for polar waters. This could be a “shock“ response to the dramatic alteration of pH and the carbonate system, before the phytoplankton community acclimate, which should be mentioned.
Also, perhaps more accurate to say the results reflect a downregulation of DMSP in temperate waters (relative to polar waters), as the mean DMSP effect is significant for both experimental time periods temperate waters in Figs 7C&D (unlike in polar waters where there is only a significant difference in the first 24 hours in Fig 7C).
Line 459 “rapid OA on DMSP producers…” more detail required here. Is this an algal physiological response or change in phytoplankton community composition?
Line 460 This paragraph is a little contradictory; starts by saying DMSP production is upregulated in polar relative to temperate, and finishes with “the lesser response seen in polar waters”
Line 466. “In an assessment across...”; this sentence should be rewritten for clarity
Line 533-540. “The polar waters sampled during our study were characterised by pronounced gradients in carbonate chemistry over small spatial scales”. Where is this shown? And what are the “small spatial scales”? The pH range of the whole voyage (“along each cruise track”) is mentioned but theres no information provided on the length of these transects which makes its difficult to compare the pH gradient between regions, or assess how significant the pH spatial gradients are. Phytoplankton won’t experience the total pH range measured on a voyage, as their exposure will be limited by physical constraints such as currents and water masses. Furthermore, the sites sampled within each voyage will experience different pH variability. The information on the drivers of spatial gradients (in paragraph Line 541-554) is interesting, but theres no indication of the spatial scale associated with this to relate spatial pH gradients to phytoplankton. The authors have provided some examples of the temporal pH variation at certain sites (Paragraph Line 555-564), but these do not consider all pH data available (for example, Beare et al (2013) show large variation (7.8-8.5) in the central North Sea). The authors supply supporting evidence from other experiments that polar phytoplankton are relatively insensitive to variation in pH, but to support their hypothesis that the regional variation in pH is the primary factor driving differences in DMSP response, more evidence and analysis of differences in regional pH variability are required.

Beare, D., McQuatters-Gollop, A., van der Hammen, T., Machiels, M., Teoh, S. J., & Hall-Spencer, J. M. (2013). Long-term trends in calcifying plankton and pH in the North Sea. PLoS One, 8(5), e61175.

Line 634 Section 4.4. This section should highly other benefits of mesocosms (inclusion of larger components of the foodweb and physical factors (mixing, stratification, particle export) that are excluded from microcosms, and note that their longer duration & more holistic/inclusive framework makes mesocosm results more relevant for Earth System models. This section should also consider the shock effect of sharply altering pH in microcosms

Line 722. “Our findings contrast with two previous studies…..” this sentence (the reasons for differences in previous polar microcosm responses) should be expanded on in the Discussion section

Technical corrections/Minor comments
Introduction
Line 52-66; why does this paragraph focus on pack ice & associated climate-related changes?
Line 113 “‘winners vs loser’ dynamic”: this requires some explanation
Line 137 “Polar” not required in this sentence as the paper presents experiments from temperate waters as well as polar

Methods
Line 183. For the Drake Passage and Weddell Sea experiments suggest the Fe experiments are not mentioned (as their results aren’t discussed), and the same notation is used as for the other experiments (High CO2, High CO2 +, etc)
Line 215-219. A 48-hour experiment seems very short; however, as pointed out growth rates are faster in temperate waters than polar incubations. The authors may want to use these differential growth rates to justify the comparison of response of shorter duration temperate experiments & longer duration polar experiments.
Line 211. IF the high frequency results are not discussed them exclude this from the Methods

Results
Fig 2. As DMS & DMSP results (G-I) are only presented to depths of 100m, the non-DMS/P parameters (A-F) should be only shown for this depth range, particularly as only the surface values for non-DMS/P variables are discussed in the Results section. Currently details of the depth profiles in A-F are not visible due to the extended vertical axis used.
Fig 2. The depth profiles on DMS/P are not really discussed; the maxima is not always at the surface and these sub-surface maxima appear to be associated chl-a subsurface maxima
Line 344. This description is misleading; both the 48-hr and 96-hr samples were collected within the incubation period
Line 351 Fig 5 is DMSP data, not Fig 4
Line 372 The unpublished temperate data are an important component of this paper and so the Suppl. Table 2 data should instead be a Figure in the main paper (possibly including comparison with the publ. data from Hopkins& Archer (2014)).
Line 388. “effect” missing

Discussion
Line 487 “For all Arctic stations …”; Drake Passage & the Weddell sea are not in the Arctic
Line 698-702. These two sentences don’t seem to address the topic of Section 4.4, or this paragraph and should perhaps be moved elsewhere in the text

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ED: Publish subject to minor revisions (review by editor) (18 Nov 2019) by Katja Fennel

AR by Frances Hopkins on behalf of the Authors (27 Nov 2019) Author's response Manuscript

ED: Publish as is (28 Nov 2019) by Katja Fennel

AR by Frances Hopkins on behalf of the Authors (03 Dec 2019) Manuscript

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Short summary

We investigated the effects of ocean acidification (OA) on the production of climate active gas dimethylsulfide (DMS) in polar waters. We found that polar DMS production was unaffected by OA – in contrast to temperate waters, where large increases in DMS occurred. The regional differences in DMS response may reflect natural variability in community adaptation to ambient carbonate chemistry and should be taken into account in predicting the influence of future DMS emissions on Earth's climate.