the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
| 19 May 2021
Geophysical and biogeochemical observations using BGC Argo floats in the western North Pacific during late winter and early spring, Part 2: Biological processes during restratification periods in the euphotic and twilight layers
Abstract. Two Argo floats equipped with oxygen, chlorophyll (Chl), backscatter, and nitrate sensors conducted daily vertical profiles of the water column from a depth of 2000 m to the sea surface in the western North Pacific from January to April of 2018. Data for calibrating each sensor were obtained via shipboard sampling that occurred when the floats were deployed and recovered. Float backscatter observations were converted to particulate organic carbon (POC) concentrations using an empirical relationship derived from contemporaneous float profiles of backscatter and shipboard observations of suspended organic carbon particles. During the float deployment periods, repeated meteorological disturbances (storms) passed over the study area and caused the mixed layer to deepen. During these events, nitrate was entrained from deeper layers into the surface mixed layer, while Chl and POC in the surface mixed layer were redistributed into deeper layers. After the storms, the upper layer gradually restratified, nitrate concentrations in the surface layer decreased, and Chl and POC concentrations increased. When the floats observed the same water mass, the net community production within the euphotic layer (0–70 m), determined from the increases in POC, was 126–664 mg C m−2 d−1 (10.5–55.3 mmol C m−2 d−1) close to the values reported from a nearby area. The C/N ratio of the increase in POC and the decrease in nitrate was closed to the Redfield ratio, which indicates that the sensors were able to observe the net biochemical processes in this area despite the relatively low concentrations of nitrate and POC. To determine the fate of particles transported from the surface ocean to the twilight layer, the ratio of oxygen consumption and nitrate regeneration rates were compared. This O2/N ratio approached the Redfield ratio when the floats followed the same water mass continuously, but the consumption rate of POC was significantly lower than what would be expected based on the oxygen consumption and nitrate release rates. This suggests that dissolved organic carbon was the main substrate for the respiration in the twilight layer.
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RC1: 'Comment on bg-2021-116', Anonymous Referee #1, 28 May 2021
Review of Sukigara et al.’s manuscript
Sukigara and co-authors investigate the effect of passing storms on the production of organic matter and its fate once exported into the mesopelagic, using 2 BGC-Argo floats deployed in the western North Pacific. Main conclusions are (1) storms induced a net community production of 126-664 mg C m-2 d-1 and (2) the subsurface deviation of POC/O2/N ratios from Redfield ratios is due to remineralization of DOC which is assumed to be the main substrate. I think that the figures and results presented in the manuscript do not support these conclusions. Main issues are:
(1) BGC-Argo floats are not Lagrangian floats, so sections of oceanic properties have to be interpreted with caution. Observed changes are not necessarily temporal changes, as the float can move across different water masses. This is particularly true in highly energetic regions such as the Kuroshio Extension region. Calculating production or consumption rates requires that the floats track the same water masse. Here, the authors acknowledge that for 3 of the 4 events analysed, floats may have been tracking different water masses due to the presence of eddies. So how can we trust the production/consumption estimates? Also, when calculating these rates, it is worth mentioning that you neglect diffusive fluxes of O2 and NO3.
(2) POC production is not equivalent to net community production (NCP), as a fraction of the fixed carbon is released as DOC (22 to 40% in the North Atlantic, Alkire et al. 2012). NCP is also different from NPP (NCP=NPP-heterotrophic respiration), so it makes no sense to compare your POC production to NPP. Also, you argue that deviation from the Redfield ratio in the mesopelagic is due to remineralization of DOC (and not only POC). But the same argument stands for the C/N ratio in the surface layer. Production of POC alone is not supposed to reflect the total N consumption. See also comments on the Redfield ratio in the section below.
(3) The authors refer throughout the manuscript to temperature, salinity, wind, net heat flux and SSH, but none of these variables are shown. I understand that some of these variables are probably shown in the companion paper, but it is a bit frustrating not seeing them. You could at least show temperature and salinity sections.
(4) Regarding the form, I think the results section contains only ‘basic’ observations/results, while most important results are drowned in the discussion. The most interesting figure (figure 7), from my point of view, is only introduced and discussed in the conclusion. Also, I think a statement of the objectives of this study is missing in the abstract. I found the quality of the writing to considerably decrease over the course of the paper. I had difficulties to understand some of the discussion/conclusion sentences. The writing clearly needs to be improved.
Further detailed comments are listed below:
line 26: How do you calculate the euphotic depth? From what data?
lines 27-29: I am not sure to understand this sentence. Do you validate the quality of the sensor by comparing your C/N ratio to the Redfield ratio? If your ratio was significantly different from the Redfield one, would you conclude that the difference is due to the sensor quality or accuracy? Several studies actually demonstrated that organic matter exhibits widely varying proportions of carbon and nutrients, partly reflecting seasonal and spatial changes of the phytoplankton community structure (Green & Sambrotto 2006, Weber and Deutsch 2010, Martiny et al 2013,…). So, I think comparing your local ratio with the global average Redfield one is not very conclusive.
line 72: add biomass or concentration, “increase in phytoplankton biomass”.
line 72: “lower depths” or deeper depths?
lines 129-130: the presence or absence of optical spikes depends, among other things, on the vertical resolution of acquisition. It is pretty obvious that POC profiles from discrete water samples will have no spikes. Your sentence makes no sense.
lines 135-136: not clear to me.
lines 131-150: this paragraph should be moved to the Methods section.
line 143: Rembauvile instead of Rambauvill.
line 144: “went south to 32N”, not true.
line 167: ”there was no exposure of”, exposure to what?, not clear.
lines 170-171: is it temporal or spatial variation? as the floats moved ~300 km northward.
line 171: what is the middle layer?
line 177: respiration also occurs in the euphotic layer.
lines 185-190: not clear from the figure. Maybe the colorbar of the figure should be adjusted to better see the variations.
lines 200-202: not clear from the figure.
lines 207-208: “Chl values increased slightly in the surface layer after the deepening of the mixed layer”, where? it is not clear from the figure.
lines 208-209: phytoplankton stock can also increase during winter mixing, not only once mixing ceases. This is not visible from Chla concentration records due to dilution when the MLD deepens, but it is from depth-integrated biomass records.
lines 218-221: You are comparing local POC to Chla ratios with worldwide Cphyto to Chla ratios. That makes no sense (average phyto contribution to POC is ~30%). It is a weak demonstration that Cphyto is correlated to POC. I recommend the authors to refer to publications that investigated the Cphyto-POC(bbp) relationship (Behrenfeld et al 2005, Martinez-Vincente 2012,2013).
line 242: The link to the Japan Meteorological Agency homepage is useless. It is more appropriate to show direct wind or net heat flux records.
line 244: “it would shoal rapidly between disturbances”, why? Are net heat fluxes positive during this period? No data shown.
line 254: POC production was 126-664 mg C m-2 d-1. Does this range of values correspond to the 4 events from both floats? Which one is the most intense? and why? Comparing these values with NPP from another study makes no sense (see my general comments).
line 261: “replacement of water masses”, what do you mean by “replacement”?
line 265: “After each storm, the near-surface layer in Case 4…”. Is it true for each storm or only case 4?
line 272: What is a “time-series cross-section of nitrate profiles”?
line 275: “a closed environment”. This term is not appropriate.
lines 285-286: “the warm water mass on the west side”, which one? No temperature data.
lines 299-302: This sentence is beyond understanding.
lines 352-353: What is a “stable” water mass? What do you mean? Also, see my previous comments about the Redfield ratio.
Most of the sentences in the conclusion are not clear and have to be reformulated.
Citation: https://doi.org/10.5194/bg-2021-116-RC1 -
AC1: 'Reply on RC1', Chiho Sukigara, 20 Jul 2021
Reply for Referee #1
Thank you for your kindly comments concerning the manuscript entitled “Geophysical and biogeochemical observations using BGC Argo floats in the western North Pacific during late winter and early spring, Part 2: Biological processes during restratification periods in the euphotic and twilight layer” which we submitted for publication in Biogeosciences. We are studying all your comments carefully and reply to your comments as follows.
Main issues are:
(1) BGC-Argo floats are not Lagrangian floats, so sections of oceanic properties have to be interpreted with caution. Observed changes are not necessarily temporal changes, as the float can move across different water masses. This is particularly true in highly energetic regions such as the Kuroshio Extension region. Calculating production or consumption rates requires that the floats track the same water masse. Here, the authors acknowledge that for 3 of the 4 events analysed, floats may have been tracking different water masses due to the presence of eddies. So how can we trust the production/consumption estimates? Also, when calculating these rates, it is worth mentioning that you neglect diffusive fluxes of O2 and NO3.
Author Comment (AC): As you pointed out, we focused on four evens (Case 1 to 4) and discussed their biogeochemical changes. Of those, Case 4 was the only one which we could trace the same water mass. We should have discussed the physical processes of the water mass before we discuss the biogeochemical processes. In the revised manuscript, we will revise it to include an enough physical discussion. Also, we calculated the net flux of O2 and NO3. Therefore, we cannot calculate diffusive fluxes of O2 and NO3, but we did not ignore them.
(2) POC production is not equivalent to net community production (NCP), as a fraction of the fixed carbon is released as DOC (22 to 40% in the North Atlantic, Alkire et al. 2012). NCP is also different from NPP (NCP=NPP-heterotrophic respiration), so it makes no sense to compare your POC production to NPP. Also, you argue that deviation from the Redfield ratio in the mesopelagic is due to remineralization of DOC (and not only POC). But the same argument stands for the C/N ratio in the surface layer. Production of POC alone is not supposed to reflect the total N consumption. See also comments on the Redfield ratio in the section below.
AC: Thank you for your comment. I understood that we were estimating POC production and not NPP or NCP. In the revised manuscript, we will discuss the estimate of POC production. And we will compare it to the CN ratios reported in the past, considering DOC production.
(3) The authors refer throughout the manuscript to temperature, salinity, wind, net heat flux and SSH, but none of these variables are shown. I understand that some of these variables are probably shown in the companion paper, but it is a bit frustrating not seeing them. You could at least show temperature and salinity sections.
AC: Thank you for your comment. I the revised manuscript, we will add figures of temporal variation of water temperature, salinity, and heat flux and explain them as well.
(4) Regarding the form, I think the results section contains only ‘basic’ observations/results, while most important results are drowned in the discussion. The most interesting figure (figure 7), from my point of view, is only introduced and discussed in the conclusion. Also, I think a statement of the objectives of this study is missing in the abstract. I found the quality of the writing to considerably decrease over the course of the paper. I had difficulties to understand some of the discussion/conclusion sentences. The writing clearly needs to be improved.
AC: I appreciate your comments. For figure 7, we will explain the temporal variations about materials (O2, POC, NO3) and discuss the degradation process in the twilight layer in the discussion section. We will add the objective of this study in the abstract. We will rewrite the manuscript and make it more readable.
Further detailed comments are listed below:
line 26: How do you calculate the euphotic depth? From what data?
AC: Since our CTD was equipped with a PAR sensor, we used the data to determine the depth of the euphotic layer. We will describe this in the revised manuscript.
lines 27-29: I am not sure to understand this sentence. Do you validate the quality of the sensor by comparing your C/N ratio to the Redfield ratio? If your ratio was significantly different from the Redfield one, would you conclude that the difference is due to the sensor quality or accuracy? Several studies actually demonstrated that organic matter exhibits widely varying proportions of carbon and nutrients, partly reflecting seasonal and spatial changes of the phytoplankton community structure (Green & Sambrotto 2006, Weber and Deutsch 2010, Martiny et al 2013,…). So, I think comparing your local ratio with the global average Redfield one is not very conclusive.
AC: We considered the sensor corrections to be approximately current because the ratio of the decrease in nitrate to the increase in POC obtained by the two independent sensors was on the same order of magnitude as the Redfield ratio when the sensors observed in the same water mass. However, we also understand that CN ratio can vary with region and season. In the revised manuscript, we will compare the CN ratios with those reported in the past.
line 72: add biomass or concentration, “increase in phytoplankton biomass”.
AC: We will add “20 ug chl.a m-2” to the revised masucript.
line 72: “lower depths” or deeper depths?
Ac: “deeper depths”. I will rewrite them.
lines 129-130: the presence or absence of optical spikes depends, among other things, on the vertical resolution of acquisition. It is pretty obvious that POC profiles from discrete water samples will have no spikes. Your sentence makes no sense.
AC: We will delete this sentence.
lines 135-136: not clear to me.
AC: These sentences are not so important. So, we will delete these sentences.
lines 131-150: this paragraph should be moved to the Methods section.
AC: We will move these paragraphs to the Methods section.
line 143: Rembauvile instead of Rambauvill.
AC: I am sorry. We will rewrite the name.
line 144: “went south to 32N”, not true.
AC: We will rewrite to “32.4N”.
line 167: ”there was no exposure of”, exposure to what?, not clear.
AC: The word “exposure” meant that the 25.3 sigma-theta water mass did not come to the surface of the ocean. We will rewrite this sentence.
lines 170-171: is it temporal or spatial variation? as the floats moved ~300 km northward.
AC: We described this sentence in terms of temporal variation. However, we will add a description of spatial variation as well.
line 171: what is the middle layer?
AC: We wrote “the middle layer” to mean “below the euphotic layer”. We will rewrite it as ““below the euphotic layer”.
line 177: respiration also occurs in the euphotic layer.
AC: It was an inaccurate sentence. we would rewrite “beneath the euphotic zone” as “throughout the water column”.
lines 185-190: not clear from the figure. Maybe the colorbar of the figure should be adjusted to better see the variations.
AC: We will redraw figures. The coloring will be adjusted.
lines 200-202: not clear from the figure.
AC: We will add some marks in figures to indicate where we focus.
lines 207-208: “Chl values increased slightly in the surface layer after the deepening of the mixed layer”, where? it is not clear from the figure.
AC: We will add some marks in figures to indicate where we focus.
lines 208-209: phytoplankton stock can also increase during winter mixing, not only once mixing ceases. This is not visible from Chla concentration records due to dilution when the MLD deepens, but it is from depth-integrated biomass records.
AC: We will integrate Chla to the deepest mixed layer depth during the observation period, and discuss that as well.
lines 218-221: You are comparing local POC to Chla ratios with worldwide Cphyto to Chla ratios. That makes no sense (average phyto contribution to POC is ~30%). It is a weak demonstration that Cphyto is correlated to POC. I recommend the authors to refer to publications that investigated the Cphyto-POC(bbp) relationship (Behrenfeld et al 2005, Martinez-Vincente 2012,2013).
AC: Thank you for the literature review. We will discuss the relationship between Cphyto-POC(bbp) in our results and literatures.
line 242: The link to the Japan Meteorological Agency homepage is useless. It is more appropriate to show direct wind or net heat flux records.
AC: We will add the figures of heat flux.
line 244: “it would shoal rapidly between disturbances”, why? Are net heat fluxes positive during this period? No data shown.
AC: We will add some sentences about the temporal variation of heat flux.
line 254: POC production was 126-664 mg C m-2 d-1. Does this range of values correspond to the 4 events from both floats? Which one is the most intense? and why? Comparing these values with NPP from another study makes no sense (see my general comments).
AC: 126 mg C m-2 d-1 corresponds to Case1, and 664 mg C m-2 d-1to Case4. However, values of Case1 cannot be compared because the water mass had changed during the observation. We will use only the results of Case4 for this sentence. We will also discuss the results as POC production, except the comparison with NPP from other study.
line 261: “replacement of water masses”, what do you mean by “replacement”?
AC: We used “replacement” in the sense of changing to another water mass. If it is confusing, we will change the word.
line 265: “After each storm, the near-surface layer in Case 4…”. Is it true for each storm or only case 4?
AC: We will remove “After each storm,”.
line 272: What is a “time-series cross-section of nitrate profiles”?
AC: We will remove “cross-section of”. We meant a time-series nitrate profiles as figures 3g and h.
line 275: “a closed environment”. This term is not appropriate.
AC: We will revise this sentence in the new manuscript.
lines 285-286: “the warm water mass on the west side”, which one? No temperature data.
AC: I will add new figures which show the horizontal distribution of the surface temperature.
lines 299-302: This sentence is beyond understanding.
AC: We will rewrite the description of the Redfield ratio, so these texts will also be substantially deleted or changed.
lines 352-353: What is a “stable” water mass? What do you mean? Also, see my previous comments about the Redfield ratio.
AC: We used “a stable water mass” to mean “not mixing with other water masses”. This sentence will be rewritten. Also, the description of the Redfield ratio will be rewritten.
Most of the sentences in the conclusion are not clear and have to be reformulated.
AC: We will explain Figure 7in Chapter 4.2. And in the Conclusion, we will write a clear description of what we found out in this study.
Citation: https://doi.org/10.5194/bg-2021-116-AC1
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AC1: 'Reply on RC1', Chiho Sukigara, 20 Jul 2021
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RC2: 'Comment on bg-2021-116', Anonymous Referee #2, 28 Jun 2021
The authors evaluated data from two fast-profiling BGC Argo floats in the western North Pacific, investigating phytoplankton production and remineralization in response to mixing events. While the overall approach is interesting and the data source is appropriate for the research question, there are some methodological issues that will need to be addressed.
Strengths:
- Daily profiling BGC Argo floats are a good fit for addressing the research questions posed.
- The Introduction is overall well written and to the point.
- I commend the authors on a thorough discussion of whether or not events observed by the floats (i.e., the individual mixing events) can be treated as a timeseries, i.e., whether the float followed a consistent water mass or not.
- Calibration of backscatter sensor with POC before and after float deployment.
Weaknesses:
- The most notable weakness, in my opinion, is the mixing of the nitrogen analysis (i.e., the decrease in nitrate over time) with an increase in POC as measured from optical backscatter. I would posit that these two can’t be directly related (i.e. to infer Redfield ratios, as was done in this study). Let’s take the mixed layer example: assuming that the Lagrangian assumption holds, then the decrease in nitrate over a short (~1 week) period of time after a deep mixing event would be related to all organic matter produced during that time, regardless of the fate of that organic matter. But the POC measured on any given day is not just the result of production, it is also affected by losses (due to grazing and export). These losses can’t be directly measured (at least not in the mixed layer), but the “lost” POC would also have contained nitrogen that is part of the “nitrogen budget” estimate. Therefore, the two measurements shouldn’t be directly compared or related, at least not in the sense that it is done in this manuscript, i.e., to infer a Redfield ratio.
- There is mention of chlorophyll samples being taken on the voyage, but then the fluorescence sensor does not appear to have been calibrated. Ideally, this should be done, or there should be mention of why it wasn’t/couldn’t be done. C:Chl ratios should also not be discussed if the fluorescence sensor wasn’t calibrated.
- While the beginning of the manuscript is overall well written and easy to follow, this cannot be said for section 4.2 from line 313 onwards. This section needs serious editing and revising, both in language/clarity and possibly in the approach. I can’t say I can fully follow the discussion from line 325 onwards, but it appears to me that an attempt is made to account for POC added via fragmentation of particles settling from above (?). But what about POC loss due to particles settling out of the layer of interest? Not all disappearing POC is lost due to remineralization, and only the remineralized part will be reflected in O2 and N. It is telling that the O2/N ratio observed was close to Redfield, but the C/N and C/O2 ratios were not. The first (O2/N) will reflect any organic matter that came through the depth layer under investigation and was remineralized (i.e., matter sinking down from above and being remineralized but not necessarily showing up as POC in the backscatter sensor, for example because it is too big or too small, or indeed dissolved). The POC observed in that layer (which is what presumably goes into the C/N and C/O2 ratios calculated) is likely just a fraction of all the carbon that moves through this layer, and its rate of change in a given depth layer is a combination of additions from above, sinking below, and remineralization, with only the latter reflected in the rate of change of O2 and N. Maybe this is what the authors try to allude to in the section starting at line 325, but I couldn’t quite follow the calculation relying on the Honda et al. paper. So in the very least this will need to be clarified, and quite possibly the calculation and interpretation will need to be changed. Just as was the case for the mixed layer, I don’t think the O2 and N measurements should be directly mixed with the POC measurements, so the C/N and C/O2 ratios are misleading in my opinion. And even if an attempt is made to account for the processes that cannot be measured here (such as fragmentation of particles), I doubt that this can be done with the kind of confidence required to come to the conclusion that DOC is such a strong player in the twilight zone (I can believe that in principle, but I don’t think the evidence in the data is strong enough to support this conclusion). For example, if I understand correctly and sediment trap data are being used to account for fragmentation, I would argue that the time scales of interest (likely months for the sediment trap data) and the event under investigation (which is presumably a high-sedimentation event) don’t match up, nor do the assumed intensities in particle flux.
Recommendations:
- Revise the approach to Redfield ratio calculations (see weaknesses above) for both mixed layer and twilight zone.
- For instances where the Lagrangian assumption doesn’t hold (i.e., the float crossed different water masses), any analyses that rely on the Lagrangian assumption should not be conducted. The discussion of water masses should come before any further inferences are made (move section starting at line 260 upwards and make it its own section in the Discussion, with a subheader).
- Consider using the Redfield ratio in a different way for an additional/new focus of the paper: Based on the disappearance of nitrogen in the mixed layer, one could use the Redfield ratio to calculate the carbon that was likely produced over the given time period in question. The difference between POC measured and POC produced (based on N) could be assumed to have been exported. This would be an interesting number to discuss? See Moreau et al. (2020) for an example of the calculations/approach (their Figure 3).
- Using calibrated phytoplankton fluorescence (i.e., working in units of Chl). With this, you could also evaluate the C:Chl ratio over time (e.g., after each mixing event), for example to explore light limitation and acclimation.
- Revise overall structure of discussion and re-focus the manuscript as appropriate (see comments under weaknesses and also Recommendations above)
- Conclusions need editing for clarity, and the section starting line 360 should be moved to the discussion. It is not good practice to introduce a new figure in the conclusions.
- Check the whole manuscript for grammar/English, with particular attention to the section between lines 313 and 344
Specifics:
- Lines 32/33: the conclusion regarding DOC in the twilight zone may need to be revised (see above)
- Line 64: “which cannot reach the mesopelagic zone” – unclear what that refers to? Do you mean “which cannot reach the mesopelagic zone by sinking”? Pleas clarify.
- Lines 80-83: This section doesn’t belong into the Methods. Add to introduction?
- Line 97: what time of day did the floats surface? This will be important for the use of the fluorescence data, i.e., is an NPQ (non-photochemical quenching) correction required or not?
- Lines 103-104: “…determined for each 0.01 kg m-3 of potential density…” – not sure what is meant by this? The offset for the oxygen correction is usually assumed to be constant along a profile and only drifting through time (if at all). So this is either unusual/unnecessary or poorly explained.
- Lines 129/130: The easy explanation for why there were no spikes in POC would be under-sampling? I.e., much less resolution in POC measurements relative to bbp.
- Line 131 and onwards: Did you smooth the bbp signal at all, for any of the subsequent analyses?
- Line 135: replace “seem to reflect” with “are in accordance with” for clarity.
- Line 154: “they slowed [by] for about a week”
- Line 159: insert reference for mixed layer definition
- Line 162 onwards: there seem to be 2 different mixed layers being discussed here (“the deep mixed layer” and the surface mixed layer introduced earlier) – they need to be properly referenced and distinguished; at the moment, this paragraph is confusing.
- Lines 175-190 contain quite a bit of discussion, not just results. Either revise or call the whole section “Results and Discussion” instead of “Results”.
- Lines 194-202: Make a bit clearer which statement refers to which float.
- Line 198: “which was located to the east” – it’s worth mentioning that this float also saw deeper mixing for longer.
- Lines 205-214: Was an NPQ correction done/necessary? Also consider availability of nitrate (not just light) when discussing patterns of Chl increase.
- Lines 218/219: C:Chl ratios require some sort of Chl calibration for the fluorometer. Please describe what was done for Chl. Also: rather than discussing C:Chl in bulk, you could show a timeseries as this would be interesting to explore light acclimation and limitation in the phytoplankton in response to mixing/restratification.
- Line 229: Primary productivity wasn’t directly measured here, so this is a poor choice for a header; maybe replace with “derived parameters” or something like that? More structure/subheaders in the following section would also be helpful.
- Line 236: “assuming minimal lateral advection” – but what about grazing and sinking? See major comment above under “weaknesses”.
- Lines 240-245: define what you called a “storm”, i.e., which low pressure systems qualified as a storm, and which didn’t?
- Lines 288-291: not sure what you mean here, especially in respect to the observations. This needs editing/clarification.
- Lines 314-316: Definition of depth layer and time interval in question needs to be made clearer. How was that depth interval chosen? How does it relate to the mixed layer? How do conclusions change if a different depth layer is investigated?
- Line 324: Not sure what is meant by “This is likely due to the lower expected rate of decline in POC.”?
- Line 325 onwards: What is the assumption about how fragmentation and backscatter interact?
- Lines 333-335: …”there would still be 0.02 mmol C m-3 d-1 …” – not sure what is meant by this. Should this be left behind but wasn’t measured,…?
- Line 350: replace “correcting” with “calibrating”
- Line 351/352: the word “disturbance” is rather unspecific here. Do you mean mixing event?
- Lines 360-371: This doesn’t belong into the conclusions, I suggest adding it to the discussion.
- Figure 3: It would be helpful to indicate eddy periods in the time series.
- Figure 4: The euphotic zone (according to the legend) seems to be assumed to be static at 70 m depth. This is unlikely to be true given the range in Chl concentrations, and in any case, the method for calculating the euphotic zone should be described in the methods section.
- Figures 6 and 7: Figure captions need editing.
- Tables 1 and 2: Titles should be more descriptive, e.g. indicate that the reported numbers refer to storm events, and mention what depth layer was investigated (Table 1). It should also be “Rate of change in POC/NO3-/DO” in the tables to be more specific.
References:
Moreau, S., Boyd, P. & Strutton, P. (2020). Remote assessment of the fate of phytoplankton in the Southern Ocean sea-ice zone. Nature Communications 11:3108.
Citation: https://doi.org/10.5194/bg-2021-116-RC2 -
AC2: 'Reply on RC2', Chiho Sukigara, 20 Jul 2021
Reply for Referee #2
Thank you for your kindly comments concerning the manuscript entitled “Geophysical and biogeochemical observations using BGC Argo floats in the western North Pacific during late winter and early spring, Part 2: Biological processes during restratification periods in the euphotic and twilight layer” which we submitted for publication in Biogeosciences. We are studying all your comments carefully and reply to your comments as follows.
The authors evaluated data from two fast-profiling BGC Argo floats in the western North Pacific, investigating phytoplankton production and remineralization in response to mixing events. While the overall approach is interesting and the data source is appropriate for the research question, there are some methodological issues that will need to be addressed.
Weaknesses:
- The most notable weakness, in my opinion, is the mixing of the nitrogen analysis (i.e., the decrease in nitrate over time) with an increase in POC as measured from optical backscatter. I would posit that these two can’t be directly related (i.e. to infer Redfield ratios, as was done in this study). Let’s take the mixed layer example: assuming that the Lagrangian assumption holds, then the decrease in nitrate over a short (~1 week) period of time after a deep mixing event would be related to all organic matter produced during that time, regardless of the fate of that organic matter. But the POC measured on any given day is not just the result of production, it is also affected by losses (due to grazing and export). These losses can’t be directly measured (at least not in the mixed layer), but the “lost” POC would also have contained nitrogen that is part of the “nitrogen budget” estimate. Therefore, the two measurements shouldn’t be directly compared or related, at least not in the sense that it is done in this manuscript, i.e., to infer a Redfield ratio.
AC: Thank you for pointing this out. Indeed, I had not thought about the loss of POC to deep layer. As noted in your “recommendation”, we will add a discussion of POC loss in the revised manuscript.
- There is mention of chlorophyll samples being taken on the voyage, but then the fluorescence sensor does not appear to have been calibrated. Ideally, this should be done, or there should be mention of why it wasn’t/couldn’t be done. C:Chl ratios should also not be discussed if the fluorescence sensor wasn’t calibrated.
AC: We will also add the correction of the fluorescence in the manuscript.
- While the beginning of the manuscript is overall well written and easy to follow, this cannot be said for section 4.2 from line 313 onwards. This section needs serious editing and revising, both in language/clarity and possibly in the approach. I can’t say I can fully follow the discussion from line 325 onwards, but it appears to me that an attempt is made to account for POC added via fragmentation of particles settling from above (?). But what about POC loss due to particles settling out of the layer of interest? Not all disappearing POC is lost due to remineralization, and only the remineralized part will be reflected in O2 and N. It is telling that the O2/N ratio observed was close to Redfield, but the C/N and C/O2 ratios were not. The first (O2/N) will reflect any organic matter that came through the depth layer under investigation and was remineralized (i.e., matter sinking down from above and being remineralized but not necessarily showing up as POC in the backscatter sensor, for example because it is too big or too small, or indeed dissolved). The POC observed in that layer (which is what presumably goes into the C/N and C/O2 ratios calculated) is likely just a fraction of all the carbon that moves through this layer, and its rate of change in a given depth layer is a combination of additions from above, sinking below, and remineralization, with only the latter reflected in the rate of change of O2 and N. Maybe this is what the authors try to allude to in the section starting at line 325, but I couldn’t quite follow the calculation relying on the Honda et al. paper. So in the very least this will need to be clarified, and quite possibly the calculation and interpretation will need to be changed. Just as was the case for the mixed layer, I don’t think the O2 and N measurements should be directly mixed with the POC measurements, so the C/N and C/O2 ratios are misleading in my opinion. And even if an attempt is made to account for the processes that cannot be measured here (such as fragmentation of particles), I doubt that this can be done with the kind of confidence required to come to the conclusion that DOC is such a strong player in the twilight zone (I can believe that in principle, but I don’t think the evidence in the data is strong enough to support this conclusion). For example, if I understand correctly and sediment trap data are being used to account for fragmentation, I would argue that the time scales of interest (likely months for the sediment trap data) and the event under investigation (which is presumably a high-sedimentation event) don’t match up, nor do the assumed intensities in particle flux.
AC: We appreciate your comment. We understood that we need to recalculate the POC loss in the twilight layer in the section 4.2. We will remove the discission of C/N and C/O2 ratio in this layer. Instead, we will add a discussion of the time-series variations of the vertical distribution of POC using Fig.7.
Recommendations:
- Revise the approach to Redfield ratio calculations (see weaknesses above) for both mixed layer and twilight zone.
AC: As mentioned above, we will add a discussion of POC loss in the mixed layer. Also, we will only discuss the O2/N ratio, and add a discussion of POC in the twilight layer separately.
- For instances where the Lagrangian assumption doesn’t hold (i.e., the float crossed different water masses), any analyses that rely on the Lagrangian assumption should not be conducted. The discussion of water masses should come before any further inferences are made (move section starting at line 260 upwards and make it its own section in the Discussion, with a subheader).
AC: Yes. We will restructure the manuscript as your comment.
- Consider using the Redfield ratio in a different way for an additional/new focus of the paper: Based on the disappearance of nitrogen in the mixed layer, one could use the Redfield ratio to calculate the carbon that was likely produced over the given time period in question. The difference between POC measured and POC produced (based on N) could be assumed to have been exported. This would be an interesting number to discuss? See Moreau et al. (2020) for an example of the calculations/approach (their Figure 3).
AC: Thank you for introducing the paper (Moreau et al., 2020). We will try to calculate the export of POC by referring to this paper.
- Using calibrated phytoplankton fluorescence (i.e., working in units of Chl). With this, you could also evaluate the C:Chl ratio over time (e.g., after each mixing event), for example to explore light limitation and acclimation.
AC: Yes. We will calibrate chl fluorescence data, and discuss the C:Chl ratio.
- Revise overall structure of discussion and re-focus the manuscript as appropriate (see comments under weaknesses and also Recommendations above)
AC: Yes. We agree.
- Conclusions need editing for clarity, and the section starting line 360 should be moved to the discussion. It is not good practice to introduce a new figure in the conclusions.
AC: Yes. We will move the explanation of Fig.7 to the section 4.2. And we will edit our conclusion.
- Check the whole manuscript for grammar/English, with particular attention to the section between lines 313 and 344
AC: Yes. We will get English proofreading for our manuscript.
Specifics:
- Lines 32/33: the conclusion regarding DOC in the twilight zone may need to be revised (see above)
AC: Yes. We will rewrite this part.
- Line 64: “which cannot reach the mesopelagic zone” – unclear what that refers to? Do you mean “which cannot reach the mesopelagic zone by sinking”? Pleas clarify.
AC: We will remove this part (“which cannot reach the mesopelagic zone”).
- Lines 80-83: This section doesn’t belong into the Methods. Add to introduction?
AC: Yes. We will move this part to the introduction.
- Line 97: what time of day did the floats surface? This will be important for the use of the fluorescence data, i.e., is an NPQ (non-photochemical quenching) correction required or not?
AC: Our floats were set to rise to the ocean surface before dawn. No NPQ correction would be needed this study. We add the surfacing time of floats in the revised manuscript.
- Lines 103-104: “…determined for each 0.01 kg m-3 of potential density…” – not sure what is meant by this? The offset for the oxygen correction is usually assumed to be constant along a profile and only drifting through time (if at all). So this is either unusual/unnecessary or poorly explained.
AC: We will add more explanation of the oxygen correction.
- Lines 129/130: The easy explanation for why there were no spikes in POC would be under-sampling? I.e., much less resolution in POC measurements relative to bbp.
AC: Yes, we understood. We will remove this sentence.
- Line 131 and onwards: Did you smooth the bbp signal at all, for any of the subsequent analyses?
AC: No, we did not smooth the bbp signal for our analyses.
- Line 135: replace “seem to reflect” with “are in accordance with” for clarity.
AC: Yes.
- Line 154: “they slowed [by] for about a week”
AC: We will remove “by”.
- Line 159: insert reference for mixed layer definition
AC: Yes. We will insert reference.
- Line 162 onwards: there seem to be 2 different mixed layers being discussed here (“the deep mixed layer” and the surface mixed layer introduced earlier) – they need to be properly referenced and distinguished; at the moment, this paragraph is confusing.
AC: We will add explanations about depths here.
- Lines 175-190 contain quite a bit of discussion, not just results. Either revise or call the whole section “Results and Discussion” instead of “Results”.
AC: We will consider the structure of our manuscript again.
- Lines 194-202: Make a bit clearer which statement refers to which float.
AC: Yes. We will add explanations about floats.
- Line 198: “which was located to the east” – it’s worth mentioning that this float also saw deeper mixing for longer.
AC: We will rewrite as your comment.
- Lines 205-214: Was an NPQ correction done/necessary? Also consider availability of nitrate (not just light) when discussing patterns of Chl increase.
AC: As mentioned above, no correction for NPQ is needed for this study. We will add an explanation about the availability of nitrate.
- Lines 218/219: C:Chl ratios require some sort of Chl calibration for the fluorometer. Please describe what was done for Chl. Also: rather than discussing C:Chl in bulk, you could show a timeseries as this would be interesting to explore light acclimation and limitation in the phytoplankton in response to mixing/restratification.
AC: As mentioned above, we will calibrate chl fluorescence data, and discuss the C:Chl ratio.
- Line 229: Primary productivity wasn’t directly measured here, so this is a poor choice for a header; maybe replace with “derived parameters” or something like that? More structure/subheaders in the following section would also be helpful.
AC: Yes. We were estimating POC production. In the revised manuscript, we will discuss the estimate of POC production.
- Line 236: “assuming minimal lateral advection” – but what about grazing and sinking? See major comment above under “weaknesses”.
AC: We will try to calculate the export of POC by referring to this paper.
- Lines 240-245: define what you called a “storm”, i.e., which low pressure systems qualified as a storm, and which didn’t?
AC: We will define the storm using heat flux data in the revised manuscript.
- Lines 288-291: not sure what you mean here, especially in respect to the observations. This needs editing/clarification.
AC: We will add new figures which show the horizontal distribution of the surface temperature.
- Lines 314-316: Definition of depth layer and time interval in question needs to be made clearer. How was that depth interval chosen? How does it relate to the mixed layer? How do conclusions change if a different depth layer is investigated?
AC: The chapter 4.2 will be restructured in the revised manuscript: the vertical distribution of POC will be further explained and discussed.
- Line 324: Not sure what is meant by “This is likely due to the lower expected rate of decline in POC.”?
AC: We explained that the rate of POC decrease is smaller than those of oxygen decrease and nitrate increase. In the revised manuscript, we will explain this part clearly.
- Line 325 onwards: What is the assumption about how fragmentation and backscatter interact?
AC: We had not considered about the relationship between particle fragmentation and backscatter. However, we will add a discussion of the effect of particle size on backscatter.
- Lines 333-335: …”there would still be 0.02 mmol C m-3 d-1 …” – not sure what is meant by this. Should this be left behind but wasn’t measured,…?
AC: This value is the loss rate of sinking particles, which was determined from the results of drifting sediment trap experiments conducted near the area of this study. However, as you pointed out, our results (POC decrease rate) and the trap results are not directly comparable, so this sentence will be deleted in the revised manuscript.
- Line 350: replace “correcting” with “calibrating”
AC: Yes. We will replace the word.
- Line 351/352: the word “disturbance” is rather unspecific here. Do you mean mixing event?
AC: Yes. We will rewrite “mixing event”.
- Lines 360-371: This doesn’t belong into the conclusions, I suggest adding it to the discussion.
AC: Yes. This part will be move to the discussion.
- Figure 3: It would be helpful to indicate eddy periods in the time series.
AC: Yes. We will put some marks in the Figure 3.
- Figure 4: The euphotic zone (according to the legend) seems to be assumed to be static at 70 m depth. This is unlikely to be true given the range in Chl concentrations, and in any case, the method for calculating the euphotic zone should be described in the methods section.
AC: Yes. We will add the calculation the euphotic layer in the section 2.
- Figures 6 and 7: Figure captions need editing.
AC: Yes. We will edit figures’ captions.
- Tables 1 and 2: Titles should be more descriptive, e.g. indicate that the reported numbers refer to storm events, and mention what depth layer was investigated (Table 1). It should also be “Rate of change in POC/NO3-/DO” in the tables to be more specific.
AC: Yes. We will edit tables’ titles.
Citation: https://doi.org/10.5194/bg-2021-116-AC2
Status: closed
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RC1: 'Comment on bg-2021-116', Anonymous Referee #1, 28 May 2021
Review of Sukigara et al.’s manuscript
Sukigara and co-authors investigate the effect of passing storms on the production of organic matter and its fate once exported into the mesopelagic, using 2 BGC-Argo floats deployed in the western North Pacific. Main conclusions are (1) storms induced a net community production of 126-664 mg C m-2 d-1 and (2) the subsurface deviation of POC/O2/N ratios from Redfield ratios is due to remineralization of DOC which is assumed to be the main substrate. I think that the figures and results presented in the manuscript do not support these conclusions. Main issues are:
(1) BGC-Argo floats are not Lagrangian floats, so sections of oceanic properties have to be interpreted with caution. Observed changes are not necessarily temporal changes, as the float can move across different water masses. This is particularly true in highly energetic regions such as the Kuroshio Extension region. Calculating production or consumption rates requires that the floats track the same water masse. Here, the authors acknowledge that for 3 of the 4 events analysed, floats may have been tracking different water masses due to the presence of eddies. So how can we trust the production/consumption estimates? Also, when calculating these rates, it is worth mentioning that you neglect diffusive fluxes of O2 and NO3.
(2) POC production is not equivalent to net community production (NCP), as a fraction of the fixed carbon is released as DOC (22 to 40% in the North Atlantic, Alkire et al. 2012). NCP is also different from NPP (NCP=NPP-heterotrophic respiration), so it makes no sense to compare your POC production to NPP. Also, you argue that deviation from the Redfield ratio in the mesopelagic is due to remineralization of DOC (and not only POC). But the same argument stands for the C/N ratio in the surface layer. Production of POC alone is not supposed to reflect the total N consumption. See also comments on the Redfield ratio in the section below.
(3) The authors refer throughout the manuscript to temperature, salinity, wind, net heat flux and SSH, but none of these variables are shown. I understand that some of these variables are probably shown in the companion paper, but it is a bit frustrating not seeing them. You could at least show temperature and salinity sections.
(4) Regarding the form, I think the results section contains only ‘basic’ observations/results, while most important results are drowned in the discussion. The most interesting figure (figure 7), from my point of view, is only introduced and discussed in the conclusion. Also, I think a statement of the objectives of this study is missing in the abstract. I found the quality of the writing to considerably decrease over the course of the paper. I had difficulties to understand some of the discussion/conclusion sentences. The writing clearly needs to be improved.
Further detailed comments are listed below:
line 26: How do you calculate the euphotic depth? From what data?
lines 27-29: I am not sure to understand this sentence. Do you validate the quality of the sensor by comparing your C/N ratio to the Redfield ratio? If your ratio was significantly different from the Redfield one, would you conclude that the difference is due to the sensor quality or accuracy? Several studies actually demonstrated that organic matter exhibits widely varying proportions of carbon and nutrients, partly reflecting seasonal and spatial changes of the phytoplankton community structure (Green & Sambrotto 2006, Weber and Deutsch 2010, Martiny et al 2013,…). So, I think comparing your local ratio with the global average Redfield one is not very conclusive.
line 72: add biomass or concentration, “increase in phytoplankton biomass”.
line 72: “lower depths” or deeper depths?
lines 129-130: the presence or absence of optical spikes depends, among other things, on the vertical resolution of acquisition. It is pretty obvious that POC profiles from discrete water samples will have no spikes. Your sentence makes no sense.
lines 135-136: not clear to me.
lines 131-150: this paragraph should be moved to the Methods section.
line 143: Rembauvile instead of Rambauvill.
line 144: “went south to 32N”, not true.
line 167: ”there was no exposure of”, exposure to what?, not clear.
lines 170-171: is it temporal or spatial variation? as the floats moved ~300 km northward.
line 171: what is the middle layer?
line 177: respiration also occurs in the euphotic layer.
lines 185-190: not clear from the figure. Maybe the colorbar of the figure should be adjusted to better see the variations.
lines 200-202: not clear from the figure.
lines 207-208: “Chl values increased slightly in the surface layer after the deepening of the mixed layer”, where? it is not clear from the figure.
lines 208-209: phytoplankton stock can also increase during winter mixing, not only once mixing ceases. This is not visible from Chla concentration records due to dilution when the MLD deepens, but it is from depth-integrated biomass records.
lines 218-221: You are comparing local POC to Chla ratios with worldwide Cphyto to Chla ratios. That makes no sense (average phyto contribution to POC is ~30%). It is a weak demonstration that Cphyto is correlated to POC. I recommend the authors to refer to publications that investigated the Cphyto-POC(bbp) relationship (Behrenfeld et al 2005, Martinez-Vincente 2012,2013).
line 242: The link to the Japan Meteorological Agency homepage is useless. It is more appropriate to show direct wind or net heat flux records.
line 244: “it would shoal rapidly between disturbances”, why? Are net heat fluxes positive during this period? No data shown.
line 254: POC production was 126-664 mg C m-2 d-1. Does this range of values correspond to the 4 events from both floats? Which one is the most intense? and why? Comparing these values with NPP from another study makes no sense (see my general comments).
line 261: “replacement of water masses”, what do you mean by “replacement”?
line 265: “After each storm, the near-surface layer in Case 4…”. Is it true for each storm or only case 4?
line 272: What is a “time-series cross-section of nitrate profiles”?
line 275: “a closed environment”. This term is not appropriate.
lines 285-286: “the warm water mass on the west side”, which one? No temperature data.
lines 299-302: This sentence is beyond understanding.
lines 352-353: What is a “stable” water mass? What do you mean? Also, see my previous comments about the Redfield ratio.
Most of the sentences in the conclusion are not clear and have to be reformulated.
Citation: https://doi.org/10.5194/bg-2021-116-RC1 -
AC1: 'Reply on RC1', Chiho Sukigara, 20 Jul 2021
Reply for Referee #1
Thank you for your kindly comments concerning the manuscript entitled “Geophysical and biogeochemical observations using BGC Argo floats in the western North Pacific during late winter and early spring, Part 2: Biological processes during restratification periods in the euphotic and twilight layer” which we submitted for publication in Biogeosciences. We are studying all your comments carefully and reply to your comments as follows.
Main issues are:
(1) BGC-Argo floats are not Lagrangian floats, so sections of oceanic properties have to be interpreted with caution. Observed changes are not necessarily temporal changes, as the float can move across different water masses. This is particularly true in highly energetic regions such as the Kuroshio Extension region. Calculating production or consumption rates requires that the floats track the same water masse. Here, the authors acknowledge that for 3 of the 4 events analysed, floats may have been tracking different water masses due to the presence of eddies. So how can we trust the production/consumption estimates? Also, when calculating these rates, it is worth mentioning that you neglect diffusive fluxes of O2 and NO3.
Author Comment (AC): As you pointed out, we focused on four evens (Case 1 to 4) and discussed their biogeochemical changes. Of those, Case 4 was the only one which we could trace the same water mass. We should have discussed the physical processes of the water mass before we discuss the biogeochemical processes. In the revised manuscript, we will revise it to include an enough physical discussion. Also, we calculated the net flux of O2 and NO3. Therefore, we cannot calculate diffusive fluxes of O2 and NO3, but we did not ignore them.
(2) POC production is not equivalent to net community production (NCP), as a fraction of the fixed carbon is released as DOC (22 to 40% in the North Atlantic, Alkire et al. 2012). NCP is also different from NPP (NCP=NPP-heterotrophic respiration), so it makes no sense to compare your POC production to NPP. Also, you argue that deviation from the Redfield ratio in the mesopelagic is due to remineralization of DOC (and not only POC). But the same argument stands for the C/N ratio in the surface layer. Production of POC alone is not supposed to reflect the total N consumption. See also comments on the Redfield ratio in the section below.
AC: Thank you for your comment. I understood that we were estimating POC production and not NPP or NCP. In the revised manuscript, we will discuss the estimate of POC production. And we will compare it to the CN ratios reported in the past, considering DOC production.
(3) The authors refer throughout the manuscript to temperature, salinity, wind, net heat flux and SSH, but none of these variables are shown. I understand that some of these variables are probably shown in the companion paper, but it is a bit frustrating not seeing them. You could at least show temperature and salinity sections.
AC: Thank you for your comment. I the revised manuscript, we will add figures of temporal variation of water temperature, salinity, and heat flux and explain them as well.
(4) Regarding the form, I think the results section contains only ‘basic’ observations/results, while most important results are drowned in the discussion. The most interesting figure (figure 7), from my point of view, is only introduced and discussed in the conclusion. Also, I think a statement of the objectives of this study is missing in the abstract. I found the quality of the writing to considerably decrease over the course of the paper. I had difficulties to understand some of the discussion/conclusion sentences. The writing clearly needs to be improved.
AC: I appreciate your comments. For figure 7, we will explain the temporal variations about materials (O2, POC, NO3) and discuss the degradation process in the twilight layer in the discussion section. We will add the objective of this study in the abstract. We will rewrite the manuscript and make it more readable.
Further detailed comments are listed below:
line 26: How do you calculate the euphotic depth? From what data?
AC: Since our CTD was equipped with a PAR sensor, we used the data to determine the depth of the euphotic layer. We will describe this in the revised manuscript.
lines 27-29: I am not sure to understand this sentence. Do you validate the quality of the sensor by comparing your C/N ratio to the Redfield ratio? If your ratio was significantly different from the Redfield one, would you conclude that the difference is due to the sensor quality or accuracy? Several studies actually demonstrated that organic matter exhibits widely varying proportions of carbon and nutrients, partly reflecting seasonal and spatial changes of the phytoplankton community structure (Green & Sambrotto 2006, Weber and Deutsch 2010, Martiny et al 2013,…). So, I think comparing your local ratio with the global average Redfield one is not very conclusive.
AC: We considered the sensor corrections to be approximately current because the ratio of the decrease in nitrate to the increase in POC obtained by the two independent sensors was on the same order of magnitude as the Redfield ratio when the sensors observed in the same water mass. However, we also understand that CN ratio can vary with region and season. In the revised manuscript, we will compare the CN ratios with those reported in the past.
line 72: add biomass or concentration, “increase in phytoplankton biomass”.
AC: We will add “20 ug chl.a m-2” to the revised masucript.
line 72: “lower depths” or deeper depths?
Ac: “deeper depths”. I will rewrite them.
lines 129-130: the presence or absence of optical spikes depends, among other things, on the vertical resolution of acquisition. It is pretty obvious that POC profiles from discrete water samples will have no spikes. Your sentence makes no sense.
AC: We will delete this sentence.
lines 135-136: not clear to me.
AC: These sentences are not so important. So, we will delete these sentences.
lines 131-150: this paragraph should be moved to the Methods section.
AC: We will move these paragraphs to the Methods section.
line 143: Rembauvile instead of Rambauvill.
AC: I am sorry. We will rewrite the name.
line 144: “went south to 32N”, not true.
AC: We will rewrite to “32.4N”.
line 167: ”there was no exposure of”, exposure to what?, not clear.
AC: The word “exposure” meant that the 25.3 sigma-theta water mass did not come to the surface of the ocean. We will rewrite this sentence.
lines 170-171: is it temporal or spatial variation? as the floats moved ~300 km northward.
AC: We described this sentence in terms of temporal variation. However, we will add a description of spatial variation as well.
line 171: what is the middle layer?
AC: We wrote “the middle layer” to mean “below the euphotic layer”. We will rewrite it as ““below the euphotic layer”.
line 177: respiration also occurs in the euphotic layer.
AC: It was an inaccurate sentence. we would rewrite “beneath the euphotic zone” as “throughout the water column”.
lines 185-190: not clear from the figure. Maybe the colorbar of the figure should be adjusted to better see the variations.
AC: We will redraw figures. The coloring will be adjusted.
lines 200-202: not clear from the figure.
AC: We will add some marks in figures to indicate where we focus.
lines 207-208: “Chl values increased slightly in the surface layer after the deepening of the mixed layer”, where? it is not clear from the figure.
AC: We will add some marks in figures to indicate where we focus.
lines 208-209: phytoplankton stock can also increase during winter mixing, not only once mixing ceases. This is not visible from Chla concentration records due to dilution when the MLD deepens, but it is from depth-integrated biomass records.
AC: We will integrate Chla to the deepest mixed layer depth during the observation period, and discuss that as well.
lines 218-221: You are comparing local POC to Chla ratios with worldwide Cphyto to Chla ratios. That makes no sense (average phyto contribution to POC is ~30%). It is a weak demonstration that Cphyto is correlated to POC. I recommend the authors to refer to publications that investigated the Cphyto-POC(bbp) relationship (Behrenfeld et al 2005, Martinez-Vincente 2012,2013).
AC: Thank you for the literature review. We will discuss the relationship between Cphyto-POC(bbp) in our results and literatures.
line 242: The link to the Japan Meteorological Agency homepage is useless. It is more appropriate to show direct wind or net heat flux records.
AC: We will add the figures of heat flux.
line 244: “it would shoal rapidly between disturbances”, why? Are net heat fluxes positive during this period? No data shown.
AC: We will add some sentences about the temporal variation of heat flux.
line 254: POC production was 126-664 mg C m-2 d-1. Does this range of values correspond to the 4 events from both floats? Which one is the most intense? and why? Comparing these values with NPP from another study makes no sense (see my general comments).
AC: 126 mg C m-2 d-1 corresponds to Case1, and 664 mg C m-2 d-1to Case4. However, values of Case1 cannot be compared because the water mass had changed during the observation. We will use only the results of Case4 for this sentence. We will also discuss the results as POC production, except the comparison with NPP from other study.
line 261: “replacement of water masses”, what do you mean by “replacement”?
AC: We used “replacement” in the sense of changing to another water mass. If it is confusing, we will change the word.
line 265: “After each storm, the near-surface layer in Case 4…”. Is it true for each storm or only case 4?
AC: We will remove “After each storm,”.
line 272: What is a “time-series cross-section of nitrate profiles”?
AC: We will remove “cross-section of”. We meant a time-series nitrate profiles as figures 3g and h.
line 275: “a closed environment”. This term is not appropriate.
AC: We will revise this sentence in the new manuscript.
lines 285-286: “the warm water mass on the west side”, which one? No temperature data.
AC: I will add new figures which show the horizontal distribution of the surface temperature.
lines 299-302: This sentence is beyond understanding.
AC: We will rewrite the description of the Redfield ratio, so these texts will also be substantially deleted or changed.
lines 352-353: What is a “stable” water mass? What do you mean? Also, see my previous comments about the Redfield ratio.
AC: We used “a stable water mass” to mean “not mixing with other water masses”. This sentence will be rewritten. Also, the description of the Redfield ratio will be rewritten.
Most of the sentences in the conclusion are not clear and have to be reformulated.
AC: We will explain Figure 7in Chapter 4.2. And in the Conclusion, we will write a clear description of what we found out in this study.
Citation: https://doi.org/10.5194/bg-2021-116-AC1
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AC1: 'Reply on RC1', Chiho Sukigara, 20 Jul 2021
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RC2: 'Comment on bg-2021-116', Anonymous Referee #2, 28 Jun 2021
The authors evaluated data from two fast-profiling BGC Argo floats in the western North Pacific, investigating phytoplankton production and remineralization in response to mixing events. While the overall approach is interesting and the data source is appropriate for the research question, there are some methodological issues that will need to be addressed.
Strengths:
- Daily profiling BGC Argo floats are a good fit for addressing the research questions posed.
- The Introduction is overall well written and to the point.
- I commend the authors on a thorough discussion of whether or not events observed by the floats (i.e., the individual mixing events) can be treated as a timeseries, i.e., whether the float followed a consistent water mass or not.
- Calibration of backscatter sensor with POC before and after float deployment.
Weaknesses:
- The most notable weakness, in my opinion, is the mixing of the nitrogen analysis (i.e., the decrease in nitrate over time) with an increase in POC as measured from optical backscatter. I would posit that these two can’t be directly related (i.e. to infer Redfield ratios, as was done in this study). Let’s take the mixed layer example: assuming that the Lagrangian assumption holds, then the decrease in nitrate over a short (~1 week) period of time after a deep mixing event would be related to all organic matter produced during that time, regardless of the fate of that organic matter. But the POC measured on any given day is not just the result of production, it is also affected by losses (due to grazing and export). These losses can’t be directly measured (at least not in the mixed layer), but the “lost” POC would also have contained nitrogen that is part of the “nitrogen budget” estimate. Therefore, the two measurements shouldn’t be directly compared or related, at least not in the sense that it is done in this manuscript, i.e., to infer a Redfield ratio.
- There is mention of chlorophyll samples being taken on the voyage, but then the fluorescence sensor does not appear to have been calibrated. Ideally, this should be done, or there should be mention of why it wasn’t/couldn’t be done. C:Chl ratios should also not be discussed if the fluorescence sensor wasn’t calibrated.
- While the beginning of the manuscript is overall well written and easy to follow, this cannot be said for section 4.2 from line 313 onwards. This section needs serious editing and revising, both in language/clarity and possibly in the approach. I can’t say I can fully follow the discussion from line 325 onwards, but it appears to me that an attempt is made to account for POC added via fragmentation of particles settling from above (?). But what about POC loss due to particles settling out of the layer of interest? Not all disappearing POC is lost due to remineralization, and only the remineralized part will be reflected in O2 and N. It is telling that the O2/N ratio observed was close to Redfield, but the C/N and C/O2 ratios were not. The first (O2/N) will reflect any organic matter that came through the depth layer under investigation and was remineralized (i.e., matter sinking down from above and being remineralized but not necessarily showing up as POC in the backscatter sensor, for example because it is too big or too small, or indeed dissolved). The POC observed in that layer (which is what presumably goes into the C/N and C/O2 ratios calculated) is likely just a fraction of all the carbon that moves through this layer, and its rate of change in a given depth layer is a combination of additions from above, sinking below, and remineralization, with only the latter reflected in the rate of change of O2 and N. Maybe this is what the authors try to allude to in the section starting at line 325, but I couldn’t quite follow the calculation relying on the Honda et al. paper. So in the very least this will need to be clarified, and quite possibly the calculation and interpretation will need to be changed. Just as was the case for the mixed layer, I don’t think the O2 and N measurements should be directly mixed with the POC measurements, so the C/N and C/O2 ratios are misleading in my opinion. And even if an attempt is made to account for the processes that cannot be measured here (such as fragmentation of particles), I doubt that this can be done with the kind of confidence required to come to the conclusion that DOC is such a strong player in the twilight zone (I can believe that in principle, but I don’t think the evidence in the data is strong enough to support this conclusion). For example, if I understand correctly and sediment trap data are being used to account for fragmentation, I would argue that the time scales of interest (likely months for the sediment trap data) and the event under investigation (which is presumably a high-sedimentation event) don’t match up, nor do the assumed intensities in particle flux.
Recommendations:
- Revise the approach to Redfield ratio calculations (see weaknesses above) for both mixed layer and twilight zone.
- For instances where the Lagrangian assumption doesn’t hold (i.e., the float crossed different water masses), any analyses that rely on the Lagrangian assumption should not be conducted. The discussion of water masses should come before any further inferences are made (move section starting at line 260 upwards and make it its own section in the Discussion, with a subheader).
- Consider using the Redfield ratio in a different way for an additional/new focus of the paper: Based on the disappearance of nitrogen in the mixed layer, one could use the Redfield ratio to calculate the carbon that was likely produced over the given time period in question. The difference between POC measured and POC produced (based on N) could be assumed to have been exported. This would be an interesting number to discuss? See Moreau et al. (2020) for an example of the calculations/approach (their Figure 3).
- Using calibrated phytoplankton fluorescence (i.e., working in units of Chl). With this, you could also evaluate the C:Chl ratio over time (e.g., after each mixing event), for example to explore light limitation and acclimation.
- Revise overall structure of discussion and re-focus the manuscript as appropriate (see comments under weaknesses and also Recommendations above)
- Conclusions need editing for clarity, and the section starting line 360 should be moved to the discussion. It is not good practice to introduce a new figure in the conclusions.
- Check the whole manuscript for grammar/English, with particular attention to the section between lines 313 and 344
Specifics:
- Lines 32/33: the conclusion regarding DOC in the twilight zone may need to be revised (see above)
- Line 64: “which cannot reach the mesopelagic zone” – unclear what that refers to? Do you mean “which cannot reach the mesopelagic zone by sinking”? Pleas clarify.
- Lines 80-83: This section doesn’t belong into the Methods. Add to introduction?
- Line 97: what time of day did the floats surface? This will be important for the use of the fluorescence data, i.e., is an NPQ (non-photochemical quenching) correction required or not?
- Lines 103-104: “…determined for each 0.01 kg m-3 of potential density…” – not sure what is meant by this? The offset for the oxygen correction is usually assumed to be constant along a profile and only drifting through time (if at all). So this is either unusual/unnecessary or poorly explained.
- Lines 129/130: The easy explanation for why there were no spikes in POC would be under-sampling? I.e., much less resolution in POC measurements relative to bbp.
- Line 131 and onwards: Did you smooth the bbp signal at all, for any of the subsequent analyses?
- Line 135: replace “seem to reflect” with “are in accordance with” for clarity.
- Line 154: “they slowed [by] for about a week”
- Line 159: insert reference for mixed layer definition
- Line 162 onwards: there seem to be 2 different mixed layers being discussed here (“the deep mixed layer” and the surface mixed layer introduced earlier) – they need to be properly referenced and distinguished; at the moment, this paragraph is confusing.
- Lines 175-190 contain quite a bit of discussion, not just results. Either revise or call the whole section “Results and Discussion” instead of “Results”.
- Lines 194-202: Make a bit clearer which statement refers to which float.
- Line 198: “which was located to the east” – it’s worth mentioning that this float also saw deeper mixing for longer.
- Lines 205-214: Was an NPQ correction done/necessary? Also consider availability of nitrate (not just light) when discussing patterns of Chl increase.
- Lines 218/219: C:Chl ratios require some sort of Chl calibration for the fluorometer. Please describe what was done for Chl. Also: rather than discussing C:Chl in bulk, you could show a timeseries as this would be interesting to explore light acclimation and limitation in the phytoplankton in response to mixing/restratification.
- Line 229: Primary productivity wasn’t directly measured here, so this is a poor choice for a header; maybe replace with “derived parameters” or something like that? More structure/subheaders in the following section would also be helpful.
- Line 236: “assuming minimal lateral advection” – but what about grazing and sinking? See major comment above under “weaknesses”.
- Lines 240-245: define what you called a “storm”, i.e., which low pressure systems qualified as a storm, and which didn’t?
- Lines 288-291: not sure what you mean here, especially in respect to the observations. This needs editing/clarification.
- Lines 314-316: Definition of depth layer and time interval in question needs to be made clearer. How was that depth interval chosen? How does it relate to the mixed layer? How do conclusions change if a different depth layer is investigated?
- Line 324: Not sure what is meant by “This is likely due to the lower expected rate of decline in POC.”?
- Line 325 onwards: What is the assumption about how fragmentation and backscatter interact?
- Lines 333-335: …”there would still be 0.02 mmol C m-3 d-1 …” – not sure what is meant by this. Should this be left behind but wasn’t measured,…?
- Line 350: replace “correcting” with “calibrating”
- Line 351/352: the word “disturbance” is rather unspecific here. Do you mean mixing event?
- Lines 360-371: This doesn’t belong into the conclusions, I suggest adding it to the discussion.
- Figure 3: It would be helpful to indicate eddy periods in the time series.
- Figure 4: The euphotic zone (according to the legend) seems to be assumed to be static at 70 m depth. This is unlikely to be true given the range in Chl concentrations, and in any case, the method for calculating the euphotic zone should be described in the methods section.
- Figures 6 and 7: Figure captions need editing.
- Tables 1 and 2: Titles should be more descriptive, e.g. indicate that the reported numbers refer to storm events, and mention what depth layer was investigated (Table 1). It should also be “Rate of change in POC/NO3-/DO” in the tables to be more specific.
References:
Moreau, S., Boyd, P. & Strutton, P. (2020). Remote assessment of the fate of phytoplankton in the Southern Ocean sea-ice zone. Nature Communications 11:3108.
Citation: https://doi.org/10.5194/bg-2021-116-RC2 -
AC2: 'Reply on RC2', Chiho Sukigara, 20 Jul 2021
Reply for Referee #2
Thank you for your kindly comments concerning the manuscript entitled “Geophysical and biogeochemical observations using BGC Argo floats in the western North Pacific during late winter and early spring, Part 2: Biological processes during restratification periods in the euphotic and twilight layer” which we submitted for publication in Biogeosciences. We are studying all your comments carefully and reply to your comments as follows.
The authors evaluated data from two fast-profiling BGC Argo floats in the western North Pacific, investigating phytoplankton production and remineralization in response to mixing events. While the overall approach is interesting and the data source is appropriate for the research question, there are some methodological issues that will need to be addressed.
Weaknesses:
- The most notable weakness, in my opinion, is the mixing of the nitrogen analysis (i.e., the decrease in nitrate over time) with an increase in POC as measured from optical backscatter. I would posit that these two can’t be directly related (i.e. to infer Redfield ratios, as was done in this study). Let’s take the mixed layer example: assuming that the Lagrangian assumption holds, then the decrease in nitrate over a short (~1 week) period of time after a deep mixing event would be related to all organic matter produced during that time, regardless of the fate of that organic matter. But the POC measured on any given day is not just the result of production, it is also affected by losses (due to grazing and export). These losses can’t be directly measured (at least not in the mixed layer), but the “lost” POC would also have contained nitrogen that is part of the “nitrogen budget” estimate. Therefore, the two measurements shouldn’t be directly compared or related, at least not in the sense that it is done in this manuscript, i.e., to infer a Redfield ratio.
AC: Thank you for pointing this out. Indeed, I had not thought about the loss of POC to deep layer. As noted in your “recommendation”, we will add a discussion of POC loss in the revised manuscript.
- There is mention of chlorophyll samples being taken on the voyage, but then the fluorescence sensor does not appear to have been calibrated. Ideally, this should be done, or there should be mention of why it wasn’t/couldn’t be done. C:Chl ratios should also not be discussed if the fluorescence sensor wasn’t calibrated.
AC: We will also add the correction of the fluorescence in the manuscript.
- While the beginning of the manuscript is overall well written and easy to follow, this cannot be said for section 4.2 from line 313 onwards. This section needs serious editing and revising, both in language/clarity and possibly in the approach. I can’t say I can fully follow the discussion from line 325 onwards, but it appears to me that an attempt is made to account for POC added via fragmentation of particles settling from above (?). But what about POC loss due to particles settling out of the layer of interest? Not all disappearing POC is lost due to remineralization, and only the remineralized part will be reflected in O2 and N. It is telling that the O2/N ratio observed was close to Redfield, but the C/N and C/O2 ratios were not. The first (O2/N) will reflect any organic matter that came through the depth layer under investigation and was remineralized (i.e., matter sinking down from above and being remineralized but not necessarily showing up as POC in the backscatter sensor, for example because it is too big or too small, or indeed dissolved). The POC observed in that layer (which is what presumably goes into the C/N and C/O2 ratios calculated) is likely just a fraction of all the carbon that moves through this layer, and its rate of change in a given depth layer is a combination of additions from above, sinking below, and remineralization, with only the latter reflected in the rate of change of O2 and N. Maybe this is what the authors try to allude to in the section starting at line 325, but I couldn’t quite follow the calculation relying on the Honda et al. paper. So in the very least this will need to be clarified, and quite possibly the calculation and interpretation will need to be changed. Just as was the case for the mixed layer, I don’t think the O2 and N measurements should be directly mixed with the POC measurements, so the C/N and C/O2 ratios are misleading in my opinion. And even if an attempt is made to account for the processes that cannot be measured here (such as fragmentation of particles), I doubt that this can be done with the kind of confidence required to come to the conclusion that DOC is such a strong player in the twilight zone (I can believe that in principle, but I don’t think the evidence in the data is strong enough to support this conclusion). For example, if I understand correctly and sediment trap data are being used to account for fragmentation, I would argue that the time scales of interest (likely months for the sediment trap data) and the event under investigation (which is presumably a high-sedimentation event) don’t match up, nor do the assumed intensities in particle flux.
AC: We appreciate your comment. We understood that we need to recalculate the POC loss in the twilight layer in the section 4.2. We will remove the discission of C/N and C/O2 ratio in this layer. Instead, we will add a discussion of the time-series variations of the vertical distribution of POC using Fig.7.
Recommendations:
- Revise the approach to Redfield ratio calculations (see weaknesses above) for both mixed layer and twilight zone.
AC: As mentioned above, we will add a discussion of POC loss in the mixed layer. Also, we will only discuss the O2/N ratio, and add a discussion of POC in the twilight layer separately.
- For instances where the Lagrangian assumption doesn’t hold (i.e., the float crossed different water masses), any analyses that rely on the Lagrangian assumption should not be conducted. The discussion of water masses should come before any further inferences are made (move section starting at line 260 upwards and make it its own section in the Discussion, with a subheader).
AC: Yes. We will restructure the manuscript as your comment.
- Consider using the Redfield ratio in a different way for an additional/new focus of the paper: Based on the disappearance of nitrogen in the mixed layer, one could use the Redfield ratio to calculate the carbon that was likely produced over the given time period in question. The difference between POC measured and POC produced (based on N) could be assumed to have been exported. This would be an interesting number to discuss? See Moreau et al. (2020) for an example of the calculations/approach (their Figure 3).
AC: Thank you for introducing the paper (Moreau et al., 2020). We will try to calculate the export of POC by referring to this paper.
- Using calibrated phytoplankton fluorescence (i.e., working in units of Chl). With this, you could also evaluate the C:Chl ratio over time (e.g., after each mixing event), for example to explore light limitation and acclimation.
AC: Yes. We will calibrate chl fluorescence data, and discuss the C:Chl ratio.
- Revise overall structure of discussion and re-focus the manuscript as appropriate (see comments under weaknesses and also Recommendations above)
AC: Yes. We agree.
- Conclusions need editing for clarity, and the section starting line 360 should be moved to the discussion. It is not good practice to introduce a new figure in the conclusions.
AC: Yes. We will move the explanation of Fig.7 to the section 4.2. And we will edit our conclusion.
- Check the whole manuscript for grammar/English, with particular attention to the section between lines 313 and 344
AC: Yes. We will get English proofreading for our manuscript.
Specifics:
- Lines 32/33: the conclusion regarding DOC in the twilight zone may need to be revised (see above)
AC: Yes. We will rewrite this part.
- Line 64: “which cannot reach the mesopelagic zone” – unclear what that refers to? Do you mean “which cannot reach the mesopelagic zone by sinking”? Pleas clarify.
AC: We will remove this part (“which cannot reach the mesopelagic zone”).
- Lines 80-83: This section doesn’t belong into the Methods. Add to introduction?
AC: Yes. We will move this part to the introduction.
- Line 97: what time of day did the floats surface? This will be important for the use of the fluorescence data, i.e., is an NPQ (non-photochemical quenching) correction required or not?
AC: Our floats were set to rise to the ocean surface before dawn. No NPQ correction would be needed this study. We add the surfacing time of floats in the revised manuscript.
- Lines 103-104: “…determined for each 0.01 kg m-3 of potential density…” – not sure what is meant by this? The offset for the oxygen correction is usually assumed to be constant along a profile and only drifting through time (if at all). So this is either unusual/unnecessary or poorly explained.
AC: We will add more explanation of the oxygen correction.
- Lines 129/130: The easy explanation for why there were no spikes in POC would be under-sampling? I.e., much less resolution in POC measurements relative to bbp.
AC: Yes, we understood. We will remove this sentence.
- Line 131 and onwards: Did you smooth the bbp signal at all, for any of the subsequent analyses?
AC: No, we did not smooth the bbp signal for our analyses.
- Line 135: replace “seem to reflect” with “are in accordance with” for clarity.
AC: Yes.
- Line 154: “they slowed [by] for about a week”
AC: We will remove “by”.
- Line 159: insert reference for mixed layer definition
AC: Yes. We will insert reference.
- Line 162 onwards: there seem to be 2 different mixed layers being discussed here (“the deep mixed layer” and the surface mixed layer introduced earlier) – they need to be properly referenced and distinguished; at the moment, this paragraph is confusing.
AC: We will add explanations about depths here.
- Lines 175-190 contain quite a bit of discussion, not just results. Either revise or call the whole section “Results and Discussion” instead of “Results”.
AC: We will consider the structure of our manuscript again.
- Lines 194-202: Make a bit clearer which statement refers to which float.
AC: Yes. We will add explanations about floats.
- Line 198: “which was located to the east” – it’s worth mentioning that this float also saw deeper mixing for longer.
AC: We will rewrite as your comment.
- Lines 205-214: Was an NPQ correction done/necessary? Also consider availability of nitrate (not just light) when discussing patterns of Chl increase.
AC: As mentioned above, no correction for NPQ is needed for this study. We will add an explanation about the availability of nitrate.
- Lines 218/219: C:Chl ratios require some sort of Chl calibration for the fluorometer. Please describe what was done for Chl. Also: rather than discussing C:Chl in bulk, you could show a timeseries as this would be interesting to explore light acclimation and limitation in the phytoplankton in response to mixing/restratification.
AC: As mentioned above, we will calibrate chl fluorescence data, and discuss the C:Chl ratio.
- Line 229: Primary productivity wasn’t directly measured here, so this is a poor choice for a header; maybe replace with “derived parameters” or something like that? More structure/subheaders in the following section would also be helpful.
AC: Yes. We were estimating POC production. In the revised manuscript, we will discuss the estimate of POC production.
- Line 236: “assuming minimal lateral advection” – but what about grazing and sinking? See major comment above under “weaknesses”.
AC: We will try to calculate the export of POC by referring to this paper.
- Lines 240-245: define what you called a “storm”, i.e., which low pressure systems qualified as a storm, and which didn’t?
AC: We will define the storm using heat flux data in the revised manuscript.
- Lines 288-291: not sure what you mean here, especially in respect to the observations. This needs editing/clarification.
AC: We will add new figures which show the horizontal distribution of the surface temperature.
- Lines 314-316: Definition of depth layer and time interval in question needs to be made clearer. How was that depth interval chosen? How does it relate to the mixed layer? How do conclusions change if a different depth layer is investigated?
AC: The chapter 4.2 will be restructured in the revised manuscript: the vertical distribution of POC will be further explained and discussed.
- Line 324: Not sure what is meant by “This is likely due to the lower expected rate of decline in POC.”?
AC: We explained that the rate of POC decrease is smaller than those of oxygen decrease and nitrate increase. In the revised manuscript, we will explain this part clearly.
- Line 325 onwards: What is the assumption about how fragmentation and backscatter interact?
AC: We had not considered about the relationship between particle fragmentation and backscatter. However, we will add a discussion of the effect of particle size on backscatter.
- Lines 333-335: …”there would still be 0.02 mmol C m-3 d-1 …” – not sure what is meant by this. Should this be left behind but wasn’t measured,…?
AC: This value is the loss rate of sinking particles, which was determined from the results of drifting sediment trap experiments conducted near the area of this study. However, as you pointed out, our results (POC decrease rate) and the trap results are not directly comparable, so this sentence will be deleted in the revised manuscript.
- Line 350: replace “correcting” with “calibrating”
AC: Yes. We will replace the word.
- Line 351/352: the word “disturbance” is rather unspecific here. Do you mean mixing event?
AC: Yes. We will rewrite “mixing event”.
- Lines 360-371: This doesn’t belong into the conclusions, I suggest adding it to the discussion.
AC: Yes. This part will be move to the discussion.
- Figure 3: It would be helpful to indicate eddy periods in the time series.
AC: Yes. We will put some marks in the Figure 3.
- Figure 4: The euphotic zone (according to the legend) seems to be assumed to be static at 70 m depth. This is unlikely to be true given the range in Chl concentrations, and in any case, the method for calculating the euphotic zone should be described in the methods section.
AC: Yes. We will add the calculation the euphotic layer in the section 2.
- Figures 6 and 7: Figure captions need editing.
AC: Yes. We will edit figures’ captions.
- Tables 1 and 2: Titles should be more descriptive, e.g. indicate that the reported numbers refer to storm events, and mention what depth layer was investigated (Table 1). It should also be “Rate of change in POC/NO3-/DO” in the tables to be more specific.
AC: Yes. We will edit tables’ titles.
Citation: https://doi.org/10.5194/bg-2021-116-AC2
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