This is the second revision of the manuscript titled Microbial strong organic ligand production is tightly coupled to iron in hydrothermal plumes" by Hoffman and coauthors. I was rev1 for the first revision.
I am undecided about how to proceed. On one hand, the authors replied to all my questions and introduced changes in the text, but on the other hand, most of those changes were merely cosmetic. None of the (IMO) main shortcomings of the manuscript have been corrected. I think that the data base must be published, specially the chromatographic part, but the rejection to recognize the limitations of the technique and the refusal to comment or amend the oversimplification of data and processes makes the revision process unnecessarily long and frustrating. This attitude brings a clear problem on the long run, some misconceptions are perpetuated just because they have been published. I suggest another round of revision.
1 The first matter is the “organicity” of ligands. Some lines have been added mid-way the manuscript about the possible presence of inorganic phases and erroneously these are restricted to oxyhydroxides. Why inorganic phases are necessarily “weak” ligands? I insist, CLE-AdCSV does not provide any insight about the nature of the fraction that is not labile after equilibration with a competing commercial ligand. And this is not arguable. The manuscript should clearly state that the analytical technique cannot discriminate between organic, inorganic or mixed phases and modify the abstract to reflect that the contribution of inorganic and mixed phases to the ligand concentration is likely. Such phases are described in most of the bibliography. It must also be noted that calculations of the “ligand” concentration are based in a 1:1 Fe:ligand ratio model and that in the presence of mixed phases or inorganic phases this is just a parametrization and possibly does not respond to the actual speciation.
After my comment in the initial review, no biological process, apart of siderophore release, which is clearly insufficient, has been presented as a possible source of organic ligand concentrations of tens of nM. There is no bibliography showing such ligand concentrations, even in the absence of phytoplankton. I contacted one of the first authors involved in the electrochemical speciation in hydrothermal plumes and this researcher confirmed me that despite the label of organic ligands, no test was carried out to study their “organicity”. And the whole bibliographic body about the presence of persistent inorganic phases has been either ignored or just cited ignoring the part referred to stabilized inorganic phases. The study of hydrothermal vents is complex and requires to take into account that many precipitation processes are of very slow kinetics, especially at low temperatures and that metastable (as in non thermodynamically stable) phases may be present for very long periods (I recommend a reading of Stumm and Morgan’s book). Furthermore, colloidal phases are included in the operational definition of dissolved iron from filtration by 0.2 um. The authors argue throughout the manuscript in terms of equilibrium and this is not correct for colloids. (Fitzsimmons et al., 2017) (cited when denying the possible inorganic character of the ligands) described dFe in hydrothermal plumes as a mix of two components, one of them would be inorganic oxyhydroxides that would persist even when the plume is so dilute that most of iron is background ocean dFe. Many articles argue about the presence and persistence of nanopytites. There is irony behind the use of an article titled “Hydrothermal vents as a kinetically stable source of iron-sulphide-bearing nanoparticles to the ocean” (Yücel et al., 2011) to argument the complete precipitation of inorganic iron. Nanopyrites and the onion model are also discussed in (Hawkes et al., 2013) (cited in this manuscript) when referring to components of the “inert” fraction of hydrothermal dFe. Pyrites are known for their high insolubility; aged oxyhydroxides become more and more refractories even to acidification protocols (Raiswell et al., 2010).
This discussion pertains not only to ligand concentrations but also to the so-called L1. If iron inorganic phases are organized in more or less refractory clusters, it is highly probable that SA, especially when used at such a low alpha coefficient, cannot "peel" the colloid off during the overnight equilibration. Iron not available for ligand exchange would manifest as a complex with a very high K but limited to an upper threshold. This upper limit is caused by the limitation of the analytical technique known as the analytical window that forces K (or alpha if the authors prefer) into the analytical window. The possible presence of inorganic phases and their possible inert character should be added to the abstract and throughout the manuscript and the role of siderophores toned down.
2 The use of L1 as a proxy for siderophore concentration is also at least arguable and there is not consensus in the field as the text seems to point. Recent works by Slagter, Gerringa, Laglera and Sukekava have shown that the so-called L1 is present in Arctic waters where humics are overwhelmingly the majority of ligands, and that competing desferrioxamine B only extracts a fraction of iron bound to reference humic material. The possible ascription of non siderophore ligands to the so-called L1 pool has also been recently discussed by Mahieu and co authors. It is very likely that nanopyrites and nano aged Fe oxyhydroxides may contribute to electrochemical L1 in hydrothermal plumes (this is considered in (Kleint et al., 2016) and for the case of copper complexes in (Sander et al., 2007)).
3 The weight of the role of siderophores. In their response the authors state We have edited some sections of the manuscript to make it clear that we do not think that siderophores are a major part of the L1 pool, but rather that their presence in these systems is intriguing and suggests that the other strong ligands we observed in the neutrally-buoyant plumes might also be microbially-produced (whether or not they are siderophores). This line of argument is impeccable but not compatible with this line in the introduction: “The tight coupling between strong ligands and dissolved iron within neutrally buoyant plumes across distinct hydrothermal environments, and the presence of dissolved siderophores with siderophore-producing microbial genera, suggests that biological production of ligands exerts a key control on hydrothermal dissolved iron concentrations”. Here again, it is conferred a controlling role to a group of substances found at a maximum of 4% of the ligand concentration and the possible contribution of inorganic colloids and nanoparticles, which presence is commonly accepted, completely ignored. The ecological importance of siderophores is huge but at the concentrations shown here, and in the absence of other organic candidate to contribute to organic ligands, the data base is far from even suggesting the biological control of dFe by microbial exudation or lysis products.
4 The trend to self citation has not been corrected at all. In the response, the authors argue in favour of the relevance of their bibliography and the need to keep the number of citations low. Case by case this makes sense but when I go to the bibliography and see that authors of the weight in the iron speciation community such as Gerringa and van den Berg or in the study of hydrothermal vents such as Sander are cited a single time this does not look right. A reader not specialized in the field would think that the authors here are almost the only ones worth to be cited. The result is the absence of works that do not align with their vision of the topic. More specifically, the bibliography about the presence of inorganic phases in hydrothermal plumes has been ignored or badly cited (omitting such parts).
An illustrative example was my comment about the two self citations used to support the description of iron transition in estuaries. From the early works of Boyle and Sholkovitz, many authors have used electrochemical techniques to find ligands in estuaries and made more contributions than the authors here: van den Berg, Laglera, Whitby, Yang, Muller, Waeles/Pernet Coudrier, etc, . Furthermore, many of these studies actually indicate that iron is exported from estuaries as humic complexes, therefore, implying that, if only the iron bound to strong ligands survives the estuarine transition, as the authors suggest, a significant part of humics must belong to L1.This is also discussed in (Slagter et al., 2019; Sukekava et al., 2024). I guess that since this presence of refractory DOM reduces the theoretical contribution of siderophores to the so-called L1 concentrations, citations of these articles are not in the interest of the authors.
The authors have the logical aim for this work to transcend, but I do not think that ignoring previous effort by other authors in the field and not discussing but ignoring bodies of bibliography that do not concur with their vision of the topic, is the best approach.
5 From the revised version: The strong coupling between dFe and ligands was only observed at sites where L1 ligands were detected. Some sampling locations, such as in the buoyant plume or closer to the vent orifice, contained high concentrations of weaker ligands (log KFe’,FeLcond < 12, Table S2) with no correlation to dFe. This is consistent with these environments likely being dominated by inorganic forms of Fe as hydrothermal fluids initially mix with oxygenated seawater
This is based in assuming that inorganic iron can only be ascribed to a weak ligand group. The refractory character of iron oxyhydroxides (for instance to competition by an added ligand) is obviously a matter of aging as the aggregates move from pure hydroxides (fresh ferrihydrite) to oxyhydroxides. In this process, not only iron aggregates (in the sense of increasing size) but also becomes more refractory, which also relates to the onion model by Mackey and Zirino. There are Raiswell references (Raiswell et al., 2010) where different oxyhydroxides are subjected to the same extraction protocols including acidification with a enormous range of efficiencies, almost of them low. Nanopyrites are insoluble and should also be refractory to ligand competition.
6 from the response by the authors: and all ligand parameters reported were confirmed to be within the analytical window of the SA measurements,
This is no control of quality. Please revisit classic works from Apte and van den Berg for definitions of analytical window and its extent. The alpha coefficient of FeSA defines the CENTER of the analytical window. The WIDTH of the analytical window is given by the analytical error. All ligands can only be resolved in the absence of data error. The analytical error, even if small, prevents the accurate determination of tiny concentrations of FeL (for weak ligands) or FeLad (for strong ligands) and such ligands are not properly characterized. As a result, alpha values and therefore log K values of strong ligands are forced to fall into a window (centred around alpha FeLad) and do not correspond to the real stability of the complex. This is a limitation of the technique independently of the quality of the analysis. For the case of copper titrations this is explained in (Laglera et al., 2013; Pižeta et al., 2015) and references there in. This means that ligands of alpha coefficient stronger than the upper limit of the analytical window are detected (these ligands have not exchanged iron with the added ligand) but K is brought down so alpha falls into the analytical window. Ligands of weaker alpha are simply not measured. So, that ligand solutions fall close to the alpha of the artificial ligand is not surprising. However, in this manuscript there is something else, log alpha values of ligands fall approximately from 1.3 to 4.9 (more than 4 orders of magnitude, table in supplement) and the centre of the window should be around 1.7 from 10 uM SA and K and B values from (Abualhaija and van den Berg, 2014). The upper limit of the analytical window should be around 3.7, which implies that some of the values cannot be “confirmed”.
7 Forward and reverse titrations should appear in different tables. Since the definition of the analytical window is different, the distribution of analytical error throughout the titration and the statistical weight of data during the data treatment is very different, forward and reverse titrations cannot return the same solution for the same sample if there is more than one ligand present. This is evident from works where both methods have been used in natural samples for copper (Nuester and van den Berg, 2005; Santos-Echeandía et al., 2008; Wiwit et al., 2021).
8 The bibliography of the tracked changes version has not been updated since at least the Hassler paper is missing
9 from the response to reviewers: Operationally defining classes of organic ligands by their conditional stability constant is an accepted and preferred strategy by the field in the application of CLE-AdCSV methods (Gledhill and Buck 2012).
This is simply not true. The definition and adscription of K values to classes (as in L1 siderophores, L2 HS and L3 EPS or similar) is the preferred strategy by a part of the field, mostly the authors in here. Other authors do not use it or directly challenge it (Mathieu, Laglera, Sukekava, Gerringa, Slagter recent manuscripts cited above)
10 from the response to reviewers: We are not sure which inorganic ligands the reviewer is specifically referring to, but if they are referring to the formation of inorganic iron oxy(hydro)oxides, then the CLE-AdCSV method would not artificially detect these compounds as “organic ligands” because the side reaction coefficient of these is 𝛼 = 10 or 11 which is outside of the analytical window used in this work.
The discussion about the presence of metastable phases, nanopyrite and aging of oxyhydroxides I wrote above is of relevance here. This inorganic alpha is not exactly the strength of the inorganic complexation, it is the ratio Fe3+:Fe’ . This alpha is summed to log K if the constant is referred to Fe3+ instead of Fe’. It does not make full chemical sense because includes the insoluble Fe(OH)3 as part of the inorganic complexes and therefore it cannot be used to compare organic/inorganic complexation.
11 Section amended: “Over the last few decades, observations and modelling efforts have increased our understanding about the critical role organic ligands play in the cycling, transport, and utilization of trace metals (Tagliabue et al., 2017; Buck et al., 2018; Bundy et al., 2018; Moore et al., 2021). Organic ligands in seawater have a wide range of sources, which are only just beginning to be understood, but observations suggest that microbial production of siderophores, humic-like substances and exopolysaccharides are some of the major contributors (Hassler et al. 2017), linking microbial activity to impacts on Fe cycling. For example, microbial communities can influence Fe cycling in environments ranging from hydrothermal plumes (Cowen and Bruland, 1985; Cowen et al., 1990) to the open ocean (Lauderdale et al., 2020).”
I would add the expression “in deep waters”. In upper waters there are sources of organic ligands more important than microbial production of ligands. Phytoplankton cultures and phytoplankton blooming waters have shown substantial ligand increments (Boye et al., 2005; Boye and van den Berg, 2000; Kondo et al., 2008; Laglera et al., 2020), riverine humics are also an important source of ligands in areas of the open ocean (van den Berg, Whitby, Laglera/Sukekava, Yang, Slagter/Gerringa, Muller, Dulaquais manuscripts).
With the rest of the manuscript I agree with the changes performed.
Abualhaija, M.M. and van den Berg, C.M.G., 2014. Chemical speciation of iron in seawater using catalytic cathodic stripping voltammetry with ligand competition against salicylaldoxime. Marine Chemistry, 164: 60-74.
Boye, M. et al., 2005. Major deviations of iron complexation during 22 days of a mesoscale iron enrichment in the open Southern Ocean. Marine Chemistry, 96(3-4): 257-271.
Boye, M. and van den Berg, C.M.G., 2000. Iron availability and the release of iron-complexing ligands by Emiliania huxleyi. Marine Chemistry, 70(4): 277-287.
Fitzsimmons, J.N. et al., 2017. Iron persistence in a distal hydrothermal plume supported by dissolved–particulate exchange. Nature Geoscience, 10(3): 195-201.
Hawkes, J.A., Connelly, D., Gledhill, M. and Achterberg, E.P., 2013. The stabilisation and transportation of dissolved iron from high temperature hydrothermal vent systems. Earth and Planetary Science Letters, 375: 280-290.
Kleint, C., Hawkes, J.A., Sander, S.G. and Koschinsky, A., 2016. Voltammetric investigation of hydrothermal iron speciation. Frontiers in Marine Science, 3: 75.
Kondo, Y. et al., 2008. Organic iron (III) complexing ligands during an iron enrichment experiment in the western subarctic North Pacific. Geophysical Research Letters, 35(12).
Laglera, L.M., Downes, J. and Santos-Echeandía, J., 2013. Comparison and combined use of linear and non-linear fitting for the estimation of complexing parameters from metal titrations of estuarine samples by CLE/AdCSV. Marine Chemistry, 155(0): 102-112.
Laglera, L.M. et al., 2020. Iron organic speciation during the LOHAFEX experiment: Iron ligands release under biomass control by copepod grazing. Journal of Marine Systems, 207: 103151.
Nuester, J. and van den Berg, C.M.G., 2005. Determination of metal speciation by reverse titrations. Analytical Chemistry, 77(1): 11-19.
Pižeta, I. et al., 2015. Interpretation of complexometric titration data: An intercomparison of methods for estimating models of trace metal complexation by natural organic ligands. Marine Chemistry, 173(0): 3-24.
Raiswell, R., Vu, H.P., Brinza, L. and Benning, L.G., 2010. The determination of labile Fe in ferrihydrite by ascorbic acid extraction: Methodology, dissolution kinetics and loss of solubility with age and de-watering. Chemical Geology, 278(1–2): 70-79.
Sander, S.G., Koschinsky, A., Massoth, G., Stott, M. and Hunter, K.A., 2007. Organic complexation of copper in deep-sea hydrothermal vent systems. Environmental Chemistry, 4(2): 81-89.
Santos-Echeandía, J., Laglera, L.M., Prego, R. and van den Berg, C.M.G., 2008. Copper speciation in estuarine waters by forward and reverse titrations. Marine Chemistry, 108(3-4): 148-158.
Slagter, H.A., Laglera, L.M., Sukekava, C. and Gerringa, L.J.A., 2019. Fe-binding Organic Ligands in the Humic-Rich TransPolar Drift in the Surface Arctic Ocean using Multiple Voltammetric Methods. Journal of Geophysical Research: Oceans, 124: 1491-1508.
Sukekava, C.F., Downes, J., Filella, M., Vilanova, B. and Laglera, L.M., 2024. Ligand exchange provides new insight into the role of humic substances in the marine iron cycle. Geochimica et Cosmochimica Acta, 366: 17-30.
Wiwit et al., 2021. Wide-range detection of Cu-binding organic ligands in seawater using reverse titration. Marine Chemistry, 230: 103927.
Yücel, M., Gartman, A., Chan, C.S. and Luther, G.W., 2011. Hydrothermal vents as a kinetically stable source of iron-sulphide-bearing nanoparticles to the ocean. Nature Geoscience, 4(6): 367-371. |
Review of "Microbial strong organic ligand production is tightly coupled to iron in hydrothermal plumes" by Hoffman and coauthors:
The manuscript employs a combination of classical electrochemical methods (CLE-AdCSV) to measure iron ligand concentrations in solution with novel developments in chromatographic recognition and quantification of siderophores to shed further light in our understanding of iron speciation in the ocean, in this case in the plumes of hydrothermal vents. The goal of the chromatographic section is to detect a broader range of these compounds for which a careful description of the level of confidence in the assignment of molecular formulae is described. The manuscript is well-written and accessible to specialists.
However, although the experiment planning and the resulting database are extremely valuable for the scientific community, I have strong reservations about the interpretation of the results, particularly in the electrochemical part and I am going to suggest major changes. Whole sections should be thought through using the arguments hereafter and followed by rewriting of many sections. Accordingly, I would only consider this manuscript as a letter if those changes are implemented.
My major concern with the current version is the assumption that the outcome of CLE-AdCSV represents "organic" ligands' concentration and stability constant. Unfortunately, a wrong assumption, once established, might be challenging to reverse. In waters with high terrestrial dissolved organic matter (DOM) input or significant biological activity (resulting in ligand exudation), this assumption might be close to the actual situation. However, it cannot be universally granted. The technique involves introducing an artificial ligand that equilibrates with the sample (CLE step), extracting a fraction of the iron in solution, and then measuring the concentration bound to the artificial ligand (the electrolabile fraction, the AdCSV step). If there are no sequestering natural ligands, the artificial ligand recovers the entire iron concentration, and electrolabile iron equals total. If all iron is so refractory bound that it does not exchange at all overnight in contact with the artificial ligand, the concentration of electrolabile iron is zero, and all iron is considered complexed with a stability constant that should be infinite (K~∝) but that the analytical window limitation of the technique forces to fall inside this window. Real samples exhibit an intermediate situation, with a partition between iron complexed to the original ligands and the added ligand, dependent on the concentration and stability constant of both ligands.
It is evident from this description that CLE-AdCSV cannot discriminate between organic and inorganic fractions, only between "labile" and "refractory" fractions competing for exchange with the added ligand. Historically, since the oceanographic studies in the 80s, researchers assumed that the partially exchanged fraction should mostly be of organic origin, especially since the technique was initially used for copper, which has no solubility issues. As the field started the study of iron in the 90s, this assumption was carried over and it was assumed that inorganic oxyhydroxides do not contribute to the partially exchangeable fraction, as their concentration is presumed to be very small and their stability very small compared to organic ligands. However, this is hardly compatible with the well known low solubility, formation of aggregates characterized by very different reactivity as a function of aging, estuarine trapping and open ocean scavenging suffered by iron.
It is certain that the manuscript's assumption about the organic complexation of iron in hydrothermal fluids relies on the literature. However, this stems from the assumption that CLE-AdCSV experiments exclusively determine "organic" ligands (Buck et al., 2018; Kleint et al., 2016; Sander and Koschinsky, 2011). This assumption is highly unlikely in hydrothermal waters with surges of Fe(II) at substantial concentrations. Fe(II) quickly oxidizes (hours-days at the local temperature and pH), creating stable colloids that continue to grow until reaching a size that induces precipitation. And no local nanomolar concentration of ligands can prevent this precipitation of micromolar iron. In this scenario, if the sample for CLE-AdCSV contains any inorganic phase smaller than 0.2 µm, that does not undergo complete solubilization overnight by the extracting effect of the artificial ligand, it will be counted as a ligand and labelled as "organic”. This is very unlike in this case. Some ligand concentrations presented here are of the same order of magnitude as those measured in cultures using cell growth media and an order of magnitude higher than iron ocean fertilizations. This is very suspitious.
In my opinion, considering that part of the ligands may be inorganic would explain 1) the high ligand concentrations, 2) the high correlation of ligands and dissolved iron independent of any biological variable, 3) and the high concentration of ligands in the absence of primary producers that could support the ligand production of bacteria. Actually arguing fot the presence of inorganic fractions in the definition of ligands, would drift from the current paradigm and add extra relevance to the manuscript.
Other concerns:
I know that this is quite radical but I would suggest to mend the interpretation of the voltammetric data, commenting on inorganic complexes and discussing forward and reverse and focus on the interesting chromatographic finding. The paper must be put into the context of the ecological relevance of these finding more than in the relevance for iron cycling since the siderophore concentrations found here apparently only binds a very minor fraction of the iron concentration in solution.
As I was reading I took some note that should be of interest to the editor and authors. I attach them, part are a repetition of what I stated above:
48 I find here that self-citation is a bit excessive, there are more people involved in this type of studies
53 again self-citation. There are many more studies about transition of iron from estuarine waters to the sea that so not concur with this vision. The importance of humics (that I assume from the authors’ previous publications that they consider weak ligands) has been well established in many studies (Laglera/van den Berg, Slagter, Yang and Muller studies by CLE-AdCSV and many other studies using fluorescence, coprecipitation). Other studies have found that transport is a function of the molecular weight of the ligand with prevalence of smaller fractions. The process and visions of different research groups are quite more diverse than simplified here.
60-64 please revise grammar
66 see my previous comment about organic ligands and hydrothermal fluids
71 word repetition
72-76 impressive range of sampling sites with different physicochemical conditions. This gives relevance to the manuscrit
Appendix 226……. Methods
245 the concentration of buffer is possibly wrong. It should be millimolar and not micromolar. This concentration would not buffer at all against the bicarbonate natural buffer, let alone against the huge formation of hydroxides inevitably associated to the polarographic analysis of oxygen saturated solutions. If the buffer was settled at such concentration, the analysis was carried out at pH close to 9 (Laglera et al 2016)
10 micromolar SA seems a compromise solution between the concentration suggested by Abualhaija and van den Berg (5 uM) and the concentration traditionally used by Buck and collaborators (25 uM). Since doubts about the use of SA increase (Gerringa et al BG paper) it is not clear that the effect of the Fe(SA)2 complex has been removed and not counted as L3. It would be good to show a linear titration of UV digested seawater in this condition to rule out such effect.
254 here the boric acid is at the same low concentration which makes me think that perhaps the buffer was not correctly implemented and the analysis was carried out at a very basic pH (at the surface of the electrode). For instance Hawkes et al (2013) 5 mM in each aliquot (50 mM in the paper is wrong).
What was the pH of the solution here? NN is supposed to work only at low pH (8 or less) according to the intial Gledhlii/van den Berg papers. This pH is so far away from the pK of the buffer (close to 9) and the buffer concentration so low that its buffering effect would be null. This is usually detected by changes in the peak potential. Can the authors compare peaks for this work with peaks obtained in studies with higher concentrations of buffer?
260 I could not find in Hawkes et al (2013) any reference to χmin = 0.8, χmax = 0.9, and c1high = 0.75. What are these constants and what is the implication of fixing them at this value and not other? I found them in the R script and although I am not expert in R it seems that the authors of the R routine suggested to use 0.9 or 0.8 as maximum value reached during the RV if the shape of the curve was not that of a double michaelis-menten. I know the topic of this manuscript is not to criticize such but it all looks very arbitrary to me and not sure how much change in L and K would bring a change of value here. I do not suggest to recalculate anything but the method used is a bit arbitrary in the assignment of constants.
265 onwards: I congratulate the authors for the effort to apply an internal quality criterion. This is randomly the case and improves greatly the relevance of this work.
266 why the result is called L1? Is there L2 in samples?
310 “siderophore concentrations reported here are estimates of siderophore concentrations in these environments based on ferrioxamine E.” although this is obviously a strong limitation, possibly this is the only way to move forward. In cases like this applied to concentrations obtained by means of other techniques, cconcentrations of other siderohores are reported in DFOE equivalents and not simply as nM. Hopefully, at the time to evaluate total siderophore concentrations, overestimations and underestimation may compensate but it would be interesting to evaluate whether DFOE gives sensitivities around the average for all compounds commercially available. Because if DFOE is particularly more or less sensitive to the detector, the authors would incur in substantial over or under estimations of concentrations for other siderophores. Was this considered at the time to select DFOE? A comment should be added
80 this sentence is 1) not based in a prior understanding of CLE-AdCSV in the case of 2018 Buck; as I referred before, the technique does not discriminate organic or inorganic ligands 2) not based in any experimental evidence in the case of the other two papers that are one a review and the other one a model where CLE-AdCSV ligand have been added.
83 onwards. Although the argument about complexation seems right and coherent, again a concentration of 10-90 nM ligands are 1 to two orders of magnitude higher than observed in very concentrated cultures or fertilization at any growth stage. Since hydrothermal plumes are not watermasses especially abundant in biomass, the biological release of tens of nanomols per litre of “organic” ligands is extremely unlikely. This would be energetically absurd, to release ligands for concentrations that are well over the iron requirement. That some aged/stabilized oxyhydroxides and/or iron sulphides are part of the sample is a more likely explanation.
Log K3 values around 8.8 are difficult to reconcile with what we know about analytical windows and CLE-AdCSV. This is especially true if the authors claim that can resolve ligands of log K 12-13 and 9-10 (separated 3 orders of magnitude) from the same titration. It would be a mathematical artifact
94-96. Again there is only self citations about rivers where there is no consensus about and there are available results from other groups that differ substantially with the processes described here. In any case it is good that the adjective organic dropped in this paragraph.
100-101 Again self citation. Recent evidence shows that a fraction of humics of riverine origin compete with siderophores for dFe (Slagter and Laglera papers in Arctic waters). Moreover, I insist that stabilized/growing inorganic fractions (of no biological origin) could be found in the L1 fraction and in the physicochemical conditions described here, constitute most of L1.
101-103 all these processes are no doubt present, but very unlikely to produce L1 ligands in the order of tens of nM.
107 None of the Cowen references include ligands measurements or even include the word ligand. The Lauderdale paper is a modelling paper and does not constitute empiric evidence. The bibliography does not support the argument
118-129 this section is very speculative and as such should be remarked. please remove significant since this term implies some statistics behind and this is not the case, it is just a speculation. The Hider and Kong reference is a review and only speculates about whether more products are expected. My problem here is that the paragraph is based in repeating a speculation. Other sources of L1 referred to in the bibliography do not deserve even a mention (humics, EPS, etc)
126 this calculation is addressed to increase the relevance of the paper but again is very speculative. A factor of 10 was found for overall ligands but the factor for siderophores following the evidence presented here should be 2.5. If the range in line 118 is increased ten fold, the range is 0.2-4% but it would be fairer to use a range about 0.03 to 0.1 %.
132-133 I agree but a reference would be nice here.
138-139 apart of bringing back again the argument that the technique cannot measure “organic” L1, since the contribution of siderophores to L1 is estimated by authors as 4% tops. This is less than the CLEAdCSV error, that it is very difficult to bring down to ~5%, there are simulations at different error level of copper titrations in the literature. This uncertainty and low contribution would impede any statistically robust contribution of siderophores to the coupling of L1 and dFe. For that, siderophores should be a substantial contribution to L1 and their concentrations be well above the analytical error in the determination of both dFe and L..
142-153 I like this paragraph and its finding, implying somehow more biodiversity in on-axis locations (assuming a wider variety would imply more bacterial species). The problem is that the relevance would be diminished if the last paragraph stands as it is. If the fraction of siderophores found is a minimum fraction of the total, these variabilities of small fractions would be irrelevant. I suggest to reduce the number of previous speculations and leave this paragraph as it is.
160-161. Not so surprising if most of L1 is very refractory/low bioavailable inorganic iron released by the vent and stabilized in the oxic environment. Bacteria would need to solubilize a fraction of such iron and the likely mechanism would be siderophore release.
169-170 this paragraph fits with the explanation that part of what is interpreted here as L1 is inorganic (<0.2 um) refractory iron.
175-182. I assume there were no bacteria counts in particles or free living. Particles in the ocean are hot spots of bacterial activity. It could be that this difference here in siderophore producers it is simply a matter of bacteria density.
202 In my opinion tis argument that concentrations of units to tens of nM of iron cannot be enough to suppress siderophore production. It is clearly a matter either of passive siderophore production (continuous production, and not a response to low iron concentrations) or that the bioavailability of iron is reduced which would make more sense if this is inorganic. Pleas rewrite this section
Buck, K. N., P. N. Sedwick, B. Sohst, and C. A. Carlson (2018), Organic complexation of iron in the eastern tropical South Pacific: Results from US GEOTRACES Eastern Pacific Zonal Transect (GEOTRACES cruise GP16), Mar. Chem., 201, 229-241.
Kleint, C., J. A. Hawkes, S. G. Sander, and A. Koschinsky (2016), Voltammetric investigation of hydrothermal iron speciation, Front. Mar. Sci., 3, 75.
Sander, S. G., and A. Koschinsky (2011), Metal flux from hydrothermal vents increased by organic complexation, Nature Geoscience, 4(3), 145-150.