Seasonal methane accumulation and release from a gas emission site in the central North Sea

Mau, S.; Gentz, T.; Körber, J.-H.; Torres, M. E.; Römer, M.; Sahling, H.; Wintersteller, P.; Martinez, R.; Schlüter, M.; Helmke, E.

doi:https://doi.org/10.5194/bg-12-5261-2015

Articles | Volume 12, issue 18

https://doi.org/10.5194/bg-12-5261-2015

© Author(s) 2015. This work is distributed under
the Creative Commons Attribution 3.0 License.

https://doi.org/10.5194/bg-12-5261-2015

© Author(s) 2015. This work is distributed under
the Creative Commons Attribution 3.0 License.

Articles | Volume 12, issue 18

Research article

|

16 Sep 2015

Research article |

| 16 Sep 2015

Seasonal methane accumulation and release from a gas emission site in the central North Sea

S. Mau, T. Gentz, J.-H. Körber, M. E. Torres, M. Römer, H. Sahling, P. Wintersteller, R. Martinez, M. Schlüter, and E. Helmke

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Final revised paper (published on 16 Sep 2015)
Supplement to the final revised paper
Preprint (discussion started on 19 Dec 2014)
Supplement to the preprint

Interactive discussion

Status: closed

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

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- Supplement

RC C7740: 'Referee comments for manuscript bg-2014-506, Seasonal methane accumulation and release from a gas emission site in the central North Sea', Anonymous Referee #1, 02 Jan 2015
- AC C8520: 'Response to Reviewer 1', Susan Mau, 05 Feb 2015
RC C8002: 'review to bg-2014-506', Anonymous Referee #2, 11 Jan 2015
- AC C8525: 'Response to Reviewer 2', Susan Mau, 05 Feb 2015
RC C8517: 'Seasonal methane accumulation at gas seeps in the North Sea', Anonymous Referee #3, 05 Feb 2015
- AC C8974: 'Response to Reviewer 3', Susan Mau, 06 Mar 2015
RC C8749: 'Comments on bg-2014-506', John Kessler, 13 Feb 2015
- AC C8983: 'Response to J. Kesslers review', Susan Mau, 06 Mar 2015

Peer-review completion

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

AR by Susan Mau on behalf of the Authors (09 Mar 2015) Author's response Manuscript

ED: Referee Nomination & Report Request started (18 Mar 2015) by Tina Treude

RR by Anonymous Referee #3 (13 Apr 2015)

RR by Anonymous Referee #5 (13 Apr 2015)

Suggestions for revision or reasons for rejection

Comments to revised version of Mau et al. and related reviews:

After reading the revised version of Mau et al., the supplement, and all related reviews I am convinced that the measured data set and observations should be published. Especially the summer/winter comparison of dissolved methane distributions and Mox activities are rare data sets and should be brought to public. However, my feeling is that the authors should focus on the microbial and dissolved methane studies at the gas seepage site as their oceanographic data recording was limited during their sampling campaign. In the following summary I highlight some specific issues which were also raised during the review process by the reviewers involved before.
I have no further suggestions related to reviewer#1 comments as they are fully acknowledged and the mainly microbiological and kinetic arguments are considered in the revised manuscript.
Whereas reviewer#1 is generally positive, the comments of reviewer#2 are more critical and his arguments mainly focus on the weaker part of the manuscript (the oceanographic constraints and modelling attempts).
Unfortunately, the authors failed to monitor the local oceanographic conditions during their measuring campaigns (e.g. by using ADCP, Microstructure CTD). Instead they have to rely on published (general) or estimated (modelled) current data. The missed chance to measure the current regime during sampling campaigns is a big lack of the paper, and limits a sound “methane release” story for the study site.
It is hard to compare UWMS data with Niskin bottle data. A table with Niskin CH4 data would help (Appendix). Furthermore a time vs. concentration plot for the different water depth tracks would help to understand the local (3D) concentration pattern at W2/W8 area.
The methane concentration determination by using HS-technique was performed with 55 ml seawater aliquots. It depends on the exact GC configuration, but my first guess is that detection limit is in the range of normal background levels of atmospheric methane equilibrated with seawater (2-3 nM). Could you verify that the high surface methane concentrations (around 20 nM) are not created by upscaling the ppm values from the head space to a nM concentration?
Reviewer 2 asked for CH4 concentration profile data (CTD sampling). This data should be plotted/shown (e.g. figure with concentration log-scale vs depth in an appendix).
Reviewer#3 mainly focusses on determination of rate constant and Mox activity and sees also severe problems in the box modelling and transport approaches. Many of his comments are discussed in length in the authors’ answers. Maybe these answers should also be included in the revised version to some extent?
Mox rate constant calculations based on a narrow range of methane concentration data are highly questionable (reviewer#3). This problem is still the case in the revised version.
Reviewer#3-Authors’ reply10: the reply does not help. Bubbling intensity (frequency, bubble size, CH4 init., other gases?) may vary but water column imaging with echosounding could still suggest “intense” seepage. The bubble stream must be visually observed or detailed frequency-dependent multibeam investigations are necessary to give a sound argument here. Winter and summer echosounding data should have been compared in the study!
I also agree with reviewer#4’s (Kessler) concerns about the sampling: the water sampling by discrete vertical hydrocast sampling along a straight 6 km line crossing the release sites. The chance to miss isolated CH4 plumes is extremely high, especially when sampling strategy is not adapted to tidal current direction changes, which could be perpendicular to the profile direction. Furthermore, hitting subsea targets by using a non-DP vessel in the North Sea (rough weather?) is challenging. The authors’ answer to the sampling issue is not helpful. In principle they agree, but the issue is addressed by adding a few general words in line 564 only. The sampling problem needs some more discussion by e.g. estimation of dissolved CH4 plume diameter (concentration gradients) and lateral plume shift relative from the release site during sampling.
The water column images of B13 gas flares observed during summer cruise should be presented. I wonder if echosounder signals reflecting bubble streams are also visible up to 6 m water depth in summer indicating bubbles in the upper water layer. Schroot et al., 2005 e.g. presented echosounder images of gas flares emanating from the seafloor in the same area (B13) reaching at least up to 10 meter below sea level. This is well within the upper layer and was imaged during the summer stratification period (August, 2002).
The 250 nM CH4 measured above the thermocline in July 2013 (revised version) also indicates efficient vertical methane transport into the upper water mass probably by bubbles (e.g. McGinnis et al., 2005 and 2011). It demonstrates that gas bubble transport of methane cannot be neglected in the model. Therefore initial bubble sizes and gas content should have been measured (see also referee 2).
Moreover, bubble dissolution is affected by stratification by separating micro-bubbles from main bubble streams. Microbubbles can be laterally transported within the thermocline (tides, main current regime). This is not considered by the simple box model.

Conclusion
The field data comprises a valuable data set and a proper description and discussion of all measured data (including UWMS concentration patterns, which was also asked for by rev#2 and #3) would be fine in such a paper about methane release from shallow gas pockets, dissolved methane concentration distribution in the North Sea, and CH4 degradation by Mox. However, I do not suggest publishing it with having a weak and maybe misleading box model as a bag-pack. The authors answer to the harsh criticism of reviewer#2 about their modelling approach is “Our simple model is rather thought to check if our hypothesis to explain our data is correct.” However, what does it mean when the model is incorrect or inappropriate to describe the real situation?

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RR by Anonymous Referee #6 (24 Apr 2015)

Suggestions for revision or reasons for rejection

This paper has two components, a well written component on microbial oxidation, and a poorly written component on the fate and transport of methane in which the authors try and use an overly simplistic model to interpret a sparse data set. Underlying the concern, the text is filled with numerous incorrect statements regarding bubble mediated transport that suggest the authors are far from expert in the field.

For example, on line 75, the authors state McGinnis et al (2006) showed only bubbles shallower than 100 m can reach the sea surface; however, Solomon et al. (2009) in a field study showed that bubbles from 550 m do reach the upper wave mixed layer. The author than quotes Mau et al for the SB channel that half the methane reaches the atmosphere; however, neglects that Clark et al (2000) – showed about half directly reaches the atmosphere in the near field from bubbles and near plume turbulence. And Clark et al (2000) is cited in Mau et al! However, as this paper is for seeps in 45 m, its unclear why she is incorrectly trying to argue about the fate of bubbles deeper than 45 m water based on incorrect and unstated assumptions.

There are many aspects that in general I find extremely troubling. For example, even after reviewers pointed out that turbulence transport in the ocean is not molecular (Fickian), the authors kept the formula using the well known symbol for molecular diffusion, D. I recommend no more erudite a source than wikipedia, “Fickian Diffusion” is for molecular. If you mean eddy diffusion (and you do), then DO NOT call it Fickian! This is really basic stuff (Fluid dynamics 101), and it is very alarming that after reviewers pointed it out, the authors did not understand this point.

Meanwhile, the authors have (unmeasured) ranges of kE that can realistically span an order of magnitude yet they claim that the uncertainty in their results are 25% from non-linearity in the wind gas exchange rate. This is not a reasonable uncertainty analysis, this is an effort to sweep an uncertainty that makes the overly linearized approach with no fluid dynamics data under the rug of meaningless interpretation.

Presentation is poor to highly deceptive.

For example, why represent concentrations as a whisker plot? And how can the ¼--3/4 box sit at 0 on several of the data groups, with negative concentration for the lowest quartile? Such errors make me wonder if the authors really critically reviewed the manuscript before submission.

To highlight another significant troubling concern, the in situ mass spec data were collected over a significant fraction of the tidal cycle, yet no effort was made to correct for where downstream and where upstream were at the different depths which correspond to shifts in the tidal flows. This means the contour plots (Fig. 4) likely is somewhere between meaningless and deceptive for use in an underlying a flux model, and the authors have no atmospheric data to estimate direct and indirect transfer to the atmosphere.

In fact, this is my main issue – several reviewers have pointed out that this is a complex three dimensional system with no velocity measurements, and should be modeled as 3D. The authors response was IMO unsatisfactory, and model validation is impossible as they have no atmospheric measurements. Yes, physicists model cows as spheres, but that gives absolutely no insight as to how they will bounce when dropped. The data clearly hint at complexity in the source (the intrusion at -10 m demonstrates significant bubble transport to near the surface, they have no idea of direct transport, but wave it away by claiming an exponential decrease with height, which is only true for small bubbles – but of course they have no size data. The CTD data suggests internal wave breaking, never mentioned, as a mecahanism for vertical transport.

The truth is that anyone who has worked in the North Sea knows there is significant complexity in water motions both above and below stratification. Thus, a 1-D model based on many untestable assumptions with no direct water column velocity measurements to ground it is as likely to lead to incorrect interpretation rather than a qualitatively informative interpretation.

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ED: Reconsider after major revisions (09 May 2015) by Tina Treude

Dear Susan and Coworkers,

thank you very much for submitting your revised manuscript to Biogeosciences.

After your revision, your manuscript was sent out to three referees for a second round of review. The reason for this thorough second review was that during the first review several referees raised concerns about the applied model. One referee considered the shortcomings of the model so severe that he/she rejected the manuscript.

In the second round of review, the revised manuscript was sent to one of the former referees (report #1) as well as to two new referees (report # 2 and #3). As you can read from report # 2 and #3, two referees again raised major concerns against the model approach as being too over simplified and not appropriate even just for the purpose of checking whether your hypotheses are correct. Both referees strongly suggest removing the improper model from the (valuable) dataset.

In the light of these strong criticisms raised against the model in both rounds of reviews, I can only follow the referees' advice and ask you to remove the model before resubmitting a revised version of the manuscript to Biogeosciences. All referees (past and present reviews) are confident that the dataset is strong and valuable without the model. The revised manuscript will then be sent out for a third round of review. Please be aware that after this last review, I will accept only minor revisions.

I further advice you to also carefully follow the referees' comments that are not dealing with the model; specifically the criticism/advice regarding microbial activity raised in report #1.

Some editorial comments on the manuscript:

I have a bit trouble following the argumentation that activity is low (based on a constant k') even at high methane turnover rates. At higher methane concentrations, the tracer is diluted by more unlabeled methane and hence the microbes have to be more active to turn over the same fraction of tracer in the same period of time as if the methane concentrations were lower. The relationship between high methane = high turnover vs. low methane = low turnover is healthy when concentrations lie within the linear part of the enzyme kinetics. Please check your argumentation or extend the discussion by comparing actual k' values with turnover and methane concentration to provide more clarity.

Table 2 indicates that in some incubations (24hrs) about half of your tracer/methane was turned over (rate of 840 nM/day vs CH4 of 1628 nM). Such a high tracer/methane turnover in a closed system is critical (but unfortunately sometimes unavoidable in the field), because rates might not have remained stable over the incubation period, which would lead to an underestimation of the potential rate. It would be good to shortly discuss this aspect.

I hope you are not discouraged by the criticism regarding the model. We are very much looking forward to receive your revised manuscript.

With kind regards
Tina Treude
BG Editor

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AR by Susan Mau on behalf of the Authors (19 Jun 2015) Author's response Manuscript

ED: Referee Nomination & Report Request started (02 Jul 2015) by Tina Treude

RR by Anonymous Referee #3 (13 Jul 2015)

RR by Ira Leifer (23 Jul 2015)

ED: Publish subject to minor revisions (Editor review) (23 Jul 2015) by Tina Treude

AR by Susan Mau on behalf of the Authors (28 Jul 2015) Author's response Manuscript

ED: Publish as is (01 Aug 2015) by Tina Treude

AR by Susan Mau on behalf of the Authors (26 Aug 2015)

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