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RC1: 'Peer Review bg-2020-304', Anonymous Referee #1, 08 Nov 2020
- AC1: 'Response to Reviewer 1', Erin Hotchkiss, 17 Dec 2020
RC2: 'review for the manuscript bg-2020-304', Anonymous Referee #2, 09 Nov 2020
- AC2: 'Response to Reviewer 2', Erin Hotchkiss, 17 Dec 2020

Peer-review completion

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

ED: Reconsider after major revisions (02 Feb 2021) by Gwenaël Abril

Dear authors

Thank you for the long and detailed response to the two reviewers’ comments on your MS. Please, accept my apologies for the long time necessary to take my editorial decision. The two reviewers have made numerous and significant comments, and I also found some ambiguity in your responses to these comments. Note that among the 3 evaluation criteria of the journal (scientific relevance / scientific quality / presentation quality) the reviewers have selected “fair” or “poor”. However, both recommend to reconsider your MS after major revisions. This means that your MS needs some profound revision in its structure, argumentation and presentation, before it reaches the standards of Biogeosciences and that a second round of review will be necessary.

I found very clear your response of the comments by the two reviewers on the way you have processed your data (“response to general comments”). This argumentation must appear in the Mat&Met of your revised MS. As said before, one difficulty for this decision came from your responses to the other comments that were vague in general and not always acceptable as valuable scientific arguments. This was the case for many responses to comments by both reviewers, and as editor, I would need more guaranties on your capacity to deny or integrate into the revised MS all these comments. In other word, the fact that you will “keep in mind” the comments when rewriting the MS is not a guaranty that the scientific content of these comments will be adequately integrated. More precise explanations of the planned changes would have been necessary at that step. This is why I suggest that you submit a new detailed and precise response to the reviewers together with your revised MS, as it would facilitate and accelerate the second round of review.

When making your revision, I also recommend that you keep focussed on WHAT YOUR DATA ARE TELLING, using simple and already well-defined hydrological terms (rather than “concepts”) like “base flow”, “flood”, “storms events”, “transient” versus “steady state”, eventually “pulsing”, and so on… I feel this MS is not necessarily the appropriate place for defining new “revolutionary” concepts. More maturation would probably be necessary for that. For instance, “pulsing steady state” (in your response to general comments) sounds like an oxymoron to me. There is no room for oxymoron in science.

Thank you again for submitting your interesting MS to BG, I am looking forward reading your revised soon.

With best regards

Gwenaël Abril
Biogeosciences associate editor.

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AR by Erin Hotchkiss on behalf of the Authors (12 May 2021) Author's response Author's tracked changes Manuscript

ED: Referee Nomination & Report Request started (13 May 2021) by Gwenaël Abril

RR by Anonymous Referee #1 (28 May 2021)

Suggestions for revision or reasons for rejection

Major
Overall, I appreciate the effort the authors made to clarify nearly every technical point requested by reviewers. However, it does not appear to me that the authors made any of the more major suggested changes to their analyses. Instead, they opted to defend the previous presentation of results. If this is OK with the Editor, it’s OK with me. Below I present the critical examples:
1. Instead of showing or demonstrating a sensitivity analysis of their choice for the 50% cumulative discharge threshold, they simply added lines 160–164, which more or less say, “take our word for it”. Even a simple discussion of results from a sensitivity analysis would suffice, but as written, the reader must accept the fact that the 10% and 50% choices were best. What about others who want to replicate the study? Should they use these values because they are shown here? I do not ask to be annoying to the authors and I trust they did their due diligence, but I think that by being more critical/quantitative in their choice here, they are also helping other researchers in their work, as well.
2. Similarly, I still do not understand the choice and rationale (Lines 185–187) for using the maximum/minimum as the departure baseline: “We use the maximum or minimum values instead of the median or mean because this approach allowed us to better capture the full range of average metabolism estimates in ways that summarizing pre-storm rates to means or medians would exclude”. I apologize if I am being dense, but this is hard to follow. How do maxima or minima better “capture the full range of average [conditions]” (bold and italics mine) better than means or medians? This illustrates to me that the authors did not take into consideration both reviewers’ valid point here, but instead discussed the issue away with one sentence. Would it be so hard to compare the results using mean previous conditions? It looks like it would drastically affect the results, implying strong sensitivity to method (see Figures A5–18).
3. The authors responded to the original suggestion about considering the effects of extremely small changes in magnitude as they relate to measurement uncertainty as follows: “We note that our metrics were indeed detectable relative to metabolism estimates (with low uncertainty, as shown in Fig 3, A4-A18, and supplementary data files). Consequently, we disagree that this approach “raises red flags.” I have to disagree here, especially being familiar with uncertainty measurements in GPP and ER. I have looked at the supplementary files and the uncertainty measurements that the authors apparently used: the standard error of the mean. This value will always be extremely tiny because the authors are dividing the standard deviation of estimates by the square root of 2000 (the number of MCMC runs). A better uncertainty measurement would be the standard deviation, the IQR, or the 95% credible intervals, as are most commonly presented for the output of these Bayesian models. It is not reasonable to use the standard error of the mean in this regard and I find this to be a major issue with the approach. For example, the event on 2013–05–23 has overlapping credible intervals for the maximum GPP value on 2013–05–21 (2.2–4.6) and the event (2.5–4.9) And the event on 2013–06–02 has overlapping credible intervals for the maximum GPP value on 2013–05–31 (1.9–4.8) and the event (2.2–4.1). Most events are like this. Can you really distinguish between these with confidence? This is yet another reason why I think the mean of the previous three days would be better. Not to mention, the mean would better capture ambient equilibrium conditions.

Minor
Line 96 : Please specify if NO3 is as N or not.

Referee Report: PDF

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ED: Reconsider after major revisions (26 Jul 2021) by Gwenaël Abril

Decision#2 on bg-2020-304

Dear authors

Many thanks for the revision of your paper and your interest for the Journal. First of all, please accept my apologies for the long delay in taking this decision. This delay was due in part to some difficulties in finding referees and in part to the content of the second report of referee#1, forcing me as associate editor to another detailed reading of all the submitted material. In fact, I agree with referee#1 that your responses to the majority of the comments were mostly verbal. In fact, you did not perform any new calculation in order to respond precisely and quantitatively to the major points raised by the two referees. Even worse, in some occasions, you did not perform some simple calculations that would have help your responses. This is quite surprising because you have all the necessary data for these statistical tests. It is also a problem for the publication of your paper because part of your conclusions might be wrong if the statistical analysis is not strengthened. In her/his second review, the referee#1 considers that “the authors did not take into consideration both reviewers’ valid point here, but instead discussed the issue away with one sentence.” Fortunately, she/he had the willingness to detail once again three major crucial comments about your data analysis. Your MS needs for a quantitative sensitivity analysis to make sure that the 10% and 50% cumulative discharge thresholds are appropriate so that they can be used for similar studies elsewhere; your MS needs a comparative analysis of the use of average, mean, maximum and minimum values as criteria to define the metabolic magnitude of departure (what does “summarizing pre-storm rates to means or medians would exclude” mean quantitatively?); finally your MS needs a more precise analysis of the uncertainties in metabolism calculations. If, as the referee points out, your analysis of uncertainties is based on an inappropriate criterion (the standard error of the mean, instead of other parameters listed by the referee), then the validity of your conclusions is questionable.

Because of the originality of the work presented in your MS, well within the scope of the Journal, I consider it would be very relevant to publish it in Biogeosciences. However, after the two rounds of review, it is still not clear from your responses and from the changes in the MS if your conclusions are based on a sufficiently robust statistical analysis of the data. For that reason, I would be very pleased to consider a new revised version that include detailed and quantitative responses to the three major comments by referee#1

With best regards
Gwenaël Abril

Biogeosciences associate editor

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AR by Erin Hotchkiss on behalf of the Authors (01 Dec 2021) Author's response Author's tracked changes Manuscript

ED: Publish as is (09 Dec 2021) by Gwenaël Abril