Status: final response (author comments only)
Review of Smith et al: Biogeochemical controls on wintertime ammonium accumulation in the surface layer of the Southern Ocean (Biogeosciences)
The authors present an interesting and thought-provoking study on the dynamics of ammonium cycling in the southern ocean. There are some nice new observations reported here building upon previous work by the UCT group, with the authors presenting a novel scenario for the seasonal accumulation and utilization of ammonium in surface waters. The paper however can be made more succinct, particularly in the discussion, which at times speculates far beyond what can be demonstrated from the presented data or confidently gleaned from the literature.
Introduction – Nicely sets the premise of the study but could be shortened and modified to avoid overly descriptive presentation of key concepts. Are Lines 107-123 really required in the intro? L107-152 could perhaps be more succinct but do clearly present the working premise behind the study
Methods – Some care and clarification needed in presentation of methodological details.
L177-178: Can you add approximate irradiance depths here?
L184-185: How many replicate samples were collected?
L204: Please quantify 13C addition and (presumably) your working assumption of ambient DIC concentration.
L213: Were (replicate) 2L bottles used as for NPP incubations? If not please add description
Section 3.2.1 – Please clarify the method, particularly the time period samples were left frozen for prior to analysis. L236 Clarify if the same sample was measured 3 times or whether you measured 3 replicates once each.
L233 – Please clarify procedures. How long were samples frozen?/ How long after sampling were samples analysed? What impact could this have had on NH4 concentrations? Freezing NH4 sampes is not ideal as it may lead to problems. See Degobbis (1973) (On the storage of seawater samples for ammonia determination ), though note there is no
Uptake rates – Based on L205/216 the incubations for N uptake were <6 hrs in length. However, by converting the short duration incubation length to day fraction in equation 1 the authors are extrapolating their results. Implicit in this approach is extrapolation to 24 hours from <6 hourly uptake expts. How confident are the authors that the measured rates of NPP and N uptake remain constant over the day/night cycle? Is it realistic to assume NPP or N uptake continues at the same rate around the clock? How could diel variations in N uptake impact the results? Could this extrapolation be one reason why the NPP rates are higher than reported previously (L397-399?)
L682-683: The authors conclude that NH4 production must be high, which in turn indicates that the NH4 uptake rates are likely biased by isotope dilution within the incubation and that final rates are thus low. This is not corrected for (nor apparently can it be given the experimental work undertaken) but needs to be formally acknowledged somewhere as it is a significant caveat for the overall discussion.
Units: Throughout the paper the authors report uptake rates as nM d-1. One assumes shorthand for nmol N L-1 d-1, but please clarify volumetric basis somewhere in methods section.
L286: Why not also present specific uptake rates for all nutrients individually?
Eq3 : Reliance upon specific uptake rates to calculate the f-ratio (rather than actual uptake rates) can lead to errors and/or inconsistencies with other studies. F-ratio values are very occasionally stated in the text and not in Table 1. Please include an indication in table 1
L294: An error of 4-8% when urea is included/excluded seems very low. Usually this would be higher – see Wafar et al 1995 (Wafar, M.V.M., P. Lecorre and S. L'helguen (1995). f-ratios calculated with and without urea uptake in nitrogen uptake by phytoplankton. Deep-Sea Research Part I 42(9), 1669-1674.)
L300: Correct/clarify oxidation rate units (i.e. nM d-1 = nmol N L-1 d-1)
L306: As above, does extrapolation from short term incubations to daily rates have an implication for the results? I.e any diel variability to consider?
L311: Is a 20 ml subsample a sufficiently large enough volume to accurately enumerate from? Why not settle and analyse the whole 250 ml sample?
L353: Any difference in the SST gradient between Leg S and Leg N?
Results- Generally clear and understandable but the section does have a tendency to seway into discussion. Present only the facts, leave the discussion to the Discussion section.
Discussion - The discussion is extremely long and should be shortened. Large parts of the discussion read like a literature review, presented solely for the purpose of supporting the seasonal scenario outlined by the authors and not necessarily to contextualise the observations presented here. Fundamentally, this paper presents NH4 uptake and NH4 oxidation rates from a single cruise, whereas the discussion incorporates additional cruise data and relies heavily upon literature observations to establish a new, somewhat speculative, view of NH4 cycling in the southern ocean, many aspects of which are not supported by data but only by assumption of their significance. Some sections e.g. section 5.3 can probably be deleted in their entirety as they go way beyond a discussion of the data presented here and stray into unnecessary speculation. The discussion section could probably be a standalone opinion paper or the premise for a proposal in its own right. Much is unsubstantiated (though not necessarily wrong) and some references used derive from rather different subtropical environments where the relevance of NH4 and urea can differ markedly.
L520: Based on Fig 4c alone it is not possible to say how long d15N conditions lasted
L726-733: Without supporting observations this is speculative and unsupported.
L737-747: Relevance? Without any supporting measurements its just not possible to ascertain validity of the statements presented here
L748-762: Relevance? No measurements of NH4 input are reported here so the connection is unclear.
Summary – L900 – Measurements of heterotrophic NH4 production rates are required to support the speculative scenario outlined in the discussion, not your conclusions
L911: Use of references in a ‘summary’ section. Not something I agree with personally. The statement being made here should be moved to the discussion.
Figures – Generally clear and readable
Fig 5: Please clarify what the black box in the legend represents (dark > 2.7 um) or remove.
Fig 5b: Difficult to read, may need resizing. Please also clarify % uptake by the 0.3-2.7 um size fraction (as per Fig 5a)
Fig 6 & Fig 7: Just getting to be too small to clearly read fonts etc. Please resize
Fig 8: If authors retain the long and extensive discussion then perhaps addition of approximate rates and pool sizes to Fig 8 will help.
We thank the Reviewers for their comments, which will considerably improve our manuscript. All three Reviewers acknowledged the importance of our observations from the understudied wintertime Southern Ocean and are supportive of the dataset and its interpretation being published once we have addressed their concerns. In the attached document we respond to the Reviewers' major comments (many common to all three of them), and then address their more minor concerns.
The authors present a study of ammonium cycling activity during an oceanographic cruise between Cape Town (South Africa) and the Marginal Ice Zone of the Southern Ocean. This is achieved through ship-based experiments. The authors present data that describes DIN concentration, N-assimilation and ammonium oxidation rate data. The manuscript is generally well written, citing appropriate refences in support of the arguments presented. The study addresses an area where there is genuinely very little information. The data is high quality and the insights are therefore valuable. I found the text expansive throughout; topics introduced and discussed are mostly relevant, although the level of detail frequently detracts from the focus of the study. In my view the manuscript would benefit from a considerably sharper focus of the main insights achieved, with less space/reliance dedicated to speculation and inference.
L18-37 - Abstract, and the manuscript more broadly. My view is that the abstract should focus on the new information/data presented, rather than drawing upon additional data sets to support the conclusions. The data certainly offers support for the implication presented in conclusion of this manuscript (that the Southern Ocean is a net CO2 source for half of the annual cycle). However, my view is that the authors over-reach the scope of their data to draw this conclusion.
L38 - Introduction - very detailed scene setting, perhaps overly so. Topics introduced are relevant, but expansive. The introduction would benefit from a tighter focus.
L39-49 - In the first paragraph there are 11 references. 7 of these are not in the reference list. I didn’t continue to check, but this needs to be done.
L150-152. While the stoichiometry of nutrient assimilation into organic material is relatively clear, I’m not sure that the stoichiometry of CO2 release per NH4+ regenerated is as clear. Does it then follow that the SO may be heterotrophic for half the year? Maybe this hypothesis needs some additional support?
L164 – I am curious as to why the sampling regime differed between the two legs of this cruise - Southward leg involved only surface underway samples, while the Northern leg included CTD casts. How might this inconsistency between legs affect the study (I suspect this difference related to ships logistics; I may have missed this information).
L171 – rosette mounted oxygen sensors are notorious for drifting. Was this unit calibrated?
L177-178 – are the authors confident that this difference in sample collection methods did not influence the results presented? My concern would specifically be with using the ships underway system for ammonium measurements. The pipework in these systems are far from clean (by scientific standards) and offer an extensive surface for biofilm formation. Microbes growing in such films rapidly exchange resources with their surroundings (i.e. the surface sea water supply), potentially modifying nutrient and gas concentrations. Separately, physically pumping water is likely to disrupt biological processes associated with cells/aggregates in the pumped water (pressure pulses/turbulence). Was a direct comparison between sampling methods done on concentrations/processes?
L204 – was the DIC concentration measured to confirm this enrichment, or is it assumed?
L210 - collected from ships sea-water supply – depth of 7m
L215 – presumably these concentrations were measured post-cruise to allow accurate enrichment determination? Worth stating this.
L217 – If I understand this correctly, a constant 15NH4 addition of 100nM was made to NH4+ oxidation vessels. In Fig 2, the ambient concentration was 0-0.7µM, representing an enrichment of 12-50%. If so, this could lead to a potential overestimation of nitrification rate.
L217 – why duplicate analysis (presumably logistics – I appreciate this is a lot of work)? This could limit the confidence in the statistical analysis of results.
L218 – I appreciate that carrier N needs to be added under certain circumstances in order to satisfy detection limits of analysis. However, this leads to a loss of sensitivity. Are the authors confident that their measurements were sufficiently separated from the inherent ‘noise’ of mass spec isotope analysis? Is the ambient NO2 data presented anywhere – I couldn’t see it.
L231 – I suspect that surface seawater supply pipework is a higher contamination risk than sample invasion due to temperature gradients…..
L269 – Are the authors confident that system drift was not an issue during the analysis of so many samples? From personal experience, and that of colleagues who undertake isotope measurements, batch runs of as little as 15 samples, but generally no greater than 25 are used, punctuated by standards and filter blanks. I am not familiar with system described but would be surprised if any MS system was sufficiently stable for a run of this length.
L281 – again, was DIC measured directly? Perhaps I missed this….
L306 – evidence from elsewhere would support this assumption, but a short consideration of alternative NO2 sources would perhaps be useful. In a well-mixed environment with a sufficient NO3 supply, light transitions can lead to NO2 release from phytoplankton (as well documented). By undertaking bottle incubations, such transitions do not take place thankfully, so this mechanism shouldn’t influence results (i.e. by diluting the enriched NO2 pool leading to an underestimation of NH4 oxidation rate).
L315-341 – AFC is a relatively standard analytical tool. The level of detail provided is unnecessary – refer to published methods.
L343 – ‘potential heterotrophic activity was evaluated… ‘
L342-350 – I doubt this approach can yield useful information about the NH4+ regeneration rate. Cell abundance (any type of cell) is no indication of cellular activity. While particulate material is decomposed leading to the regeneration of inorganic nutrients, the more labile material is likely to be associated with the dissolved organic pool, especially the material actively released from living phytoplankton cells during growth. I appreciate that the authors wish to get a handle on this aspect in order to build a view of regional NH4+ cycling, however I think this stretch detracts from the dataset.
L398 and onwards within results section – refs and associated text into discussion.
L1500 - Is it necessary to name the software package used to generate figures? I find the figures and their text on the small side, especially Fig 2, 4 and 5 (the latter has a great deal of information and appears rather cluttered), 7, 9.
L1532 – co plot of cell abundance with [NH4] – what’s the rationale for the co-plot? Is there a link suggested or is it to provide context?
L462 – ‘….food source available to heterotrophs…’ this statement is somewhat vague. Heterotrophs would include everything from heterotrophic protists to zooplankton and beyond. What is specifically referred to here?
L470-496. While it is important to try and constrain the factors that are significant to NH4+ cycling, my view is that there is too much reach beyond the data. It is not robust to infer process rates from cell or detrital abundance data. The foundation of the paper is the observational data surrounding NH4 assimilation and oxidation, and the new insight this provides. My main criticism of this contribution is that it reaches well beyond this data, to inferred contributions and speculation, to build the view of NH4 cycling. While this view may ultimately be proven to be reasonable, I think a stronger case needs to be made through direct observations of the inferred processes and rates.
L505 – ‘…growth temperatures of temperate and…’ attention.
L509 ‘….and west Indian…’ West.
L589 – ‘…could dampen total…’ Not sure what this means.
L639 – ‘supporting role for iron…’ This is speculation.
L659-662. Both NH4 and NO2 are intermediates in a number of microbial processes. It would be difficult to infer anything about how one process influences this balance.
L687 – The bacterial decomposition of DON leads to NH4+ regeneration. i.e. not just PON.
L692 – ‘fresh’ PON – specifically, do you mean labile material that can be readily decomposed?
L699 – this is speculation – what support is there for this statement?
L705-707 – what support is there for a link between the ratio of detrital to heterotrophic particles and the NH4 concentration?
L716 – ‘bacteria more efficient at lower temperatures..’ efficient at what? This is loose language.
L817 – I do not follow this. Is this specifically referring to grazing activity? Bacterial activity is predominantly heterotrophic and will most certainly be taking place here.
L831-856 – Is this section necessary? This aspect was not directly investigated (it needs dedicated spike experiments). This is an example of discussion and speculation that add little to the manuscript.
L857-886 – the manuscript now strays a considerable distance from the focus of the study. My view is that this section adds nothing to the discussion of the results.
L915 – Having read through the discussion I find it hard to pull out the headline from this study – there are steps forward, but they need to be stated more concisely, with less speculation and inference.
L95 – ‘consumption’ and ‘assimilation’ are used interchangeably. I’d associated consumption with phagotrophy/mixotrophy/grazing. Assimilation is technically more appropriate here as the underlying process referred to is inorganic nutrient utilisation by phototrophs (nutrient uptake, reduction where necessary and assimilation into organic molecules).
Ammonium (NH4+) is an important macronutrient in marine ecosystems and the dynamics of its production, utilisation, and regeneration are reasonably well studied within the marine microbial food web. However, how these dynamics play out in the Southern Ocean is not well understood and this is especially so during the winter months when conditions in this region are challenging due to large storms, low temperatures, limited light availability, and the presence of sea ice. In their paper, Smith et. al provide a detailed snapshot of NH4+ concentration and dynamics (uptake and oxidation rates) in the surface water and winter mixed layer during a winter voyage in the Atlantic sector, bordering the Indian sector, of the Southern Ocean. To better understand these dynamics, the authors investigate links between macronutrient concentrations, microbial community composition and biomass, net primary production, particulate organic matter, and nitrogen isotopic fractionation. This is a substantial data set to both analyse and interpret and I commend the authors for their very thorough analysis of the data and its links to the available literature on this topic.
There are, however, some weaknesses in the manuscript that need to be addressed. Most notable of these is the presentation of new results and data analysis in the discussion. Particularly Section 5.2, which presents a completely new data set of three additional cruises adjacent to the region being studied. This year-round analysis of NH4+ in Southern Ocean surface waters is indeed complementary to the current study and allows for analysis of seasonal cycling of NH4+. However, this seems like a separate paper on its own and is indeed, presented as such in this section (methods, results & discussion). In addition to this, there are also data and analysis presented in the supplement (Text S2 & S3) that appear to be critical for some of the analysis presented in the discussion and have not been presented or referenced at all in the results section.
Visualising such an extensive data set is a difficult task, but a lot of information is being presented in the figures and tables, which makes some of them very difficult to read or interpret, especially at publication size. The authors discuss implications of a better understanding of the seasonal NH4+ dynamics in the Southern Ocean but don't really explain how this present study may alter or affirm the current knowledge base. Lastly, the authors seem to focus on CO2 uptake and drawdown in the mixed layer in the introduction and conclusion but there is no real mention of this in the discussion. If the authors consider this an important implication of the research being presented and it should also be discussed.
L124-135 – NH4+ oxidisers are an important group of microorganisms in this study and are discussed in length in the discussion (L643-680), but it is never really explained what this microorganism group is composed of. Please provide some context in the introduction so the reader understands this better.
L188 – what concentration of acetone was used?
L208-9 – were these filters combusted? Storing them in combusted foil suggests they were?
L257-8 – here, the authors distinguish each of the fractionated size classes into 0.3-2.7um "picophytoplankton", >2.7um "nanophytoplankton", and >0.3um "bulk" but do not consistently use this terminology throughout the rest of the manuscript. It would aid in understanding if the manuscript was updated so that this terminology was consistently applied through the rest of the analysis and discussion (examples below).
L310 – the conventional size range for microplankton is 20-200um so this microscopic analysis of cells >5um also includes most of the nanoplankton size range.
L315 – there is no mention that the flow cytometry analysis was on cells sized <15um. It is only mentioned in the caption of Fig. 6.
L328 – it appears from the discussion (Section 5.1.2) that these "small heterotrophic cells" are being counted as heterotrophic bacteria. Is this correct? It appears to be implied from the data but not directly specified in this section of the methods.
L383 – the >2.7um size class has previously been defined as "nanophytoplankton" (see L257-8 above) so there should not be a need to redefine it with a different, albeit very similar, name.
L380-6 – there is no mention of the picophytoplankton (0.2-2.7um) size class results here.
L388-9 – the percentage contributions of POC & PON of the nanophytoplankton size class, when SD is taken into account, range from 48.8-112.4% and 19.5-120.1%, respectively. From Table 1 it appears that in the PAZ the proportion of POC in the nanophytoplankton class was 143.02%, and the PON for this class in the PFZ has a SD of 121.41%. I would question an analysis where a size-fractionated class displays values that are far greater than the bulk. Can the authors explain why the POC & PON proportions reported are higher in the >2.7um filters than the >0.3um filters? The authors may want to consider whether the way the data is being presented is appropriate.
L393 – the statistical analysis here is not mentioned in the methods and appears to be the only time difference among zones was analysed and reported. Are there significant trends with any of the other factors being assessed? This would be interesting to know.
L401 – the "small size class (0.2-2.7um)". Another example where a size class (picophytoplankton) has been redefined.
L400-402 – this is the only time where the relative contribution of the picophytoplankton size class is presented. It's not really clear why the authors have chosen to present this information in this context.
L423 – see comment above, L310, about microplankton size range.
L423 Section 4.5 – there is a very big difference in the counts presented between the microscopy (>5-10um) and flow cytometry results (<15um). If there is an overlap between the microscopy and flow cytometry of 5-10um in the nanophytoplankton range, then were there cells in the microscopy samples that were observed but not counted? Can the authors explain this discrepancy?
L445 – "small cells" have been previously defined as 0.3-2.7um (see L401) so this creates confusion by lack of consistency again.
L596-634 – there are a lot of results and correlations presented in this section that should be in the results section.
L602-5 – "0.3-2.7 um size fraction". This has already been defined by the authors as "picophytoplankton". See comment on L257-8 above.
L630-2 – where does this relationship data come from? The correlation between pennate abundance and NH4+ at the PF seems tenuous considering the low pennate count numbers and high variability of NH4+ south of the SAF.
L643-5 – the data presented here comparing NH4+ oxidation and uptake rates is not at all clear in Fig. 5.
L660-1 – this is new data again.
L685-6 – This section references the supplemental Text S2 and I can't see how these two relate. It is also not clear why the results presented in Text S2 are not presented in the results section of the manuscript as they seem to relate to Section 3.2.5 of the methods.
L688-736 – I would suggest a reassessment of this entire section on heterotrophic activity by bacteria and zooplankton. It contains a lot of of results and there are number of relationships and assumptions made that don't seem strongly correlated to the available data (e.g., L702-3 – the POC:PON relationship with zones is reported at non-significant in the results (L391-3) so I'm not sure a southward increase can be inferred, L730-732 – this assumption is made off a single data point and other stations with similar NH4+ concentrations don't show the same thing). The presentation of heterotrophic-to-photosynthetic cell ratios is misleading here because the terminology is the wrong way around. The ratio presented on the side of Fig. 7a is the ratio of photosynthetic-to-heterotrophic cells (e.g., 50.0°S is 9.6:1). Thus, it makes no sense to be discussing "higher ratios of heterotrophic-to-photosynthetic cells" when the data presented shows low ratios of photosynthetic-to-heterotrophic cells. This makes the analysis of this section very confusing.
Section 5.2 & 5.3 – comments on these sections made in the "General Comments" above.
Figures & Tables:
I found it very difficult to see all the detail on the figures and interpret them at the size presented in the printed publication. All of the overlays and contour values are quite distracting and make the figures overly complex and difficult to interpret.
Table 1 – I'm not sure how the "% of total of >2.7um" values were calculated but they don't seem to add up to the other data presented. I don't think these add anything to the analysis and should be removed.
Figure 5 – there is too much information presented on these figures. It is not clear why the percentage of NPP for the 0.3-2.7 size fraction is presented here. It's also worth noting that the y-axes are different for each sub-figure, which was not immediately clear. A lot of the data in these figures that are discussed in the manuscript, such as differences in concentrations between zones, is better displayed and easier to interpret in Table 1.
Figure 6 – microzooplankton is present on the legend in Fig. 6b, which displays flow cytometry data <15um.
Figure 9 – it is incredibly difficult to interpret this figure due to the size.
It can be helpful for the authors to provide additional commentary and background on analyses presented in the manuscript to aid the reader in their understanding. Text S1 is a good example of this. The content of Text S2 & 3 include results and discussion that seem to be integral in their analysis and should be presented in the results section.
L372 – "from <1 uM and <10 uM, respectively, in the STZ",
L741 – the starting point of the rebuttal ("However,") of the previous statements is not very clear. I would suggest using a different phrase.
L744 – "likely to be",
L757 – It's not "Finally," if the next sentence starts with "Additionally,". Reword.
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