Intact polar lipids in the water column of the eastern tropical North Pacific: abundance and structural variety of non-phosphorus lipids

Schubotz, Florence; Xie, Sitan; Lipp, Julius S.; Hinrichs, Kai-Uwe; Wakeham, Stuart G.

doi:https://doi.org/10.5194/bg-15-6481-2018

Articles | Volume 15, issue 21

https://doi.org/10.5194/bg-15-6481-2018

© Author(s) 2018. This work is distributed under
the Creative Commons Attribution 4.0 License.

https://doi.org/10.5194/bg-15-6481-2018

© Author(s) 2018. This work is distributed under
the Creative Commons Attribution 4.0 License.

Articles | Volume 15, issue 21

Research article

|

06 Nov 2018

Research article |

| 06 Nov 2018

Intact polar lipids in the water column of the eastern tropical North Pacific: abundance and structural variety of non-phosphorus lipids

Florence Schubotz, Sitan Xie, Julius S. Lipp, Kai-Uwe Hinrichs, and Stuart G. Wakeham

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Final revised paper (published on 06 Nov 2018)
Supplement to the final revised paper
Preprint (discussion started on 13 Mar 2018)
Supplement to the preprint

Interactive discussion

Status: closed

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

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RC1: 'Comments to Schubotz et al', Anonymous Referee #1, 26 Mar 2018
- AC1: 'Response to comments by reviewer #1', Florence Schubotz, 04 Jun 2018
RC2: 'Review of Schubotz et al. Diversity of intact polar lipids in the oxygen minimum zone of the Eastern Tropical North Pacific: Biogeochemical implications of non-phosphorus lipids', N.J. Bale, 30 Mar 2018
- AC1: 'Response to comments by reviewer #1', Florence Schubotz, 04 Jun 2018
- AC2: 'Response to comments by reviewer #2', Florence Schubotz, 04 Jun 2018
RC3: 'Review of Schubotz et al.', Anonymous Referee #3, 23 Apr 2018
- AC3: 'Response to comments by reviewer #3', Florence Schubotz, 04 Jun 2018
AC4: 'revised manuscript attached', Florence Schubotz, 04 Jun 2018
- AC5: 'revised supplement attached', Florence Schubotz, 04 Jun 2018

Peer-review completion

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

ED: Reconsider after major revisions (13 Jun 2018) by Markus Kienast

AR by Florence Schubotz on behalf of the Authors (01 Jul 2018) Author's response Manuscript

ED: Referee Nomination & Report Request started (06 Jul 2018) by Markus Kienast

RR by Anonymous Referee #3 (11 Aug 2018)

Suggestions for revision or reasons for rejection

I have reviewed the revised manuscript. It has improved but there remain a number of important issues that still need further attention before this manuscript can be published.

The title of the manuscript still emphasizes the “biogeochemical implications” which are actually fairly minor (see their abstract). The title also claims that it only studies lipids in the OMZ but that is not true. The term “diversity” for lipids seems odd, it is a biological term that should not be used in terms of chemical composition.

The authors have responded in an extensive way to my comments on the analytical methodology. It has become much more clear how the time-line of the analyses has been. They state that they have >10 years of experience with analysis of IPLs and I am not doubting their analytical capabilities at all. However, in the cases where they use rather unusual procedures (Soxhlet extraction of IPLs, re-analysis of IPL extracts after 7 years of storage at -20 degrees centigrade) they have to come up with evidence to back up their statements in the rebuttal and in the text (e.g. lines 195-197; “we believe”). Just the presence of labile IPLs does not mean that the distribution (i.e. relative percentage) has not changed (and it is the distribution that is the focus of the paper as explicitly mentioned in the rebuttal). The authors refer to Lengger et al. (2012) to support this statement. However, this paper uses only Bligh-Dyer extraction. Perhaps, they intended to refer to Lengger et al., Organic Geochemistry 47, 34 – 40 also published in 2012 but this paper shows that the extraction technique has a huge influence on the ratio between glyco- and phospholipids (see Figure 3 in that paper): Bligh Dyer extraction increases the relative amount of the phospholipid by a factor of ten or so. I therefore remain doubtful about the chosen methodology which in view of this is inappropriate. With respect to the storage issue: why don’t the authors show a supplementary figure showing the composition of their IPL standard mixture over time? This would at least solve this issue convincingly with scientific data and would answer my questions is a reasonable way. With respect to the response factors of the standards: I do understand that these response factors are not useful for the community since they are specific for the instrument at that specific moment in time. However, it still would be very helpful to see the change in response factors over time for each individual standard. If the standards are so stable upon storage: why are they renewed every 3 years (which is only 40% of the time between extraction and analysis)?

A second major point that is not solved in this new version is the distinction between major and minor IPLs (see Figure 4). I reiterate my previous comment: “The whole distinction between major and minor IPLs is rather artificial. It becomes especially confusing when minor IPLs are normalized on their sum which is a variable part of the IPLs as a whole. It is entirely unclear why this is done other than for “stamp collection” purposes. “. The text has now been changed to define major and minor IPLs (Lines 309-310) but this definition is rather confusing with the figure because it shows many IPL classes that are <10%. The bar plots of the minor compounds shows really weird things; sometimes there is only one IPL, sometimes none, and the most important thing is that it is normalized on something that is extremely variable (i.e. the sum of “minor” IPLs that varies between 0-20%). So, it is entirely confusing way of plotting the data. If the authors want to focus on these minor IPLs, why don’t they use the scale of the plots shown on the left of this figure (IPL relative abundance normalized on the sum of all IPLs) but use a scale that runs from 0-2% or so. That would be a much more fair way to present the data and would also eliminate some of the weird things (i.e. “minor” IPLs dominated by one IPL because in these cases the “minor” IPLs represent <1% of the total).

This issue directly relates to the problem that the authors keep on insisting in their idea that relative abundances are more important than absolute abundances. The problem they generate in that way is directly evident form their Figure 4. At station 8 archaeal IPLs represent 50-80% of the IPLs whereas this is much lower in the shallower waters. Fig. 2e shows that in the shallower waters there are a comparable or perhaps even higher number of archaeal cells. However, in the shallow waters the IPL concentration is much higher. When absolute concentrations of archaeal IPLs would be taken into consideration this discrepancy would likely not exist. Therefore, I strongly urge the authors to look at their data also in terms of absolute concentrations. Can’t they combine their measured absolute total concentrations of IPLs in 2010/2011 (which they now hardly use) with the %IPL determined in 2015 to arrive at concentration profiles for individual IPLs? That would allow a much more meaningful ecological interpretation of their extensive dataset. Of course, percentage data also provides some insight but the basic conclusion from Fig. 4 is now: the photic zone contains predominantly IPLs derived from phytoplankton whereas the IPLs in the OMZ are primarily derived from bacteria and archaea. This is hardly surprising; do we really need all these analyses to arrive at this conclusion?

I also still believe that correlating environmental parameters to relative abundances of IPLs is much less useful than to absolute concentrations. In any case, the statistical data treatment is not really used in the discussion, so this section (Lines 406-429) can be easily eliminated.

The discussion has been shortened substantially but is still lengthy. It starts with a paragraph (lines 432-459) that only reiterates previous findings in this setting. Where these previous finding can be directly related to the IPL profiles they should be mentioned there and this paragraph can be skipped. There is also overlap in Lines 468-474. I am also puzzled by the fact that in section 4.1.3 IPLs from two completely different zones (core OMZ and deep oxycline, i.e. without and with oxygen) are discussed together. The discussion of the origin of the archaeal IPLs (Lines 558-570) is fairly limited. In the upper OMZ hardly any archaeal IPLs are detected (Figure 4) so this needs explanation. Also, the reason for linking them to Group II Euryarchaeota needs argumentation.

The conclusion (line 708-711) is simply wrong. Not only oxygen is the primary determinant but also light. Without light there would not be any production of IPLs by algae and cyanobacteria, quantitatively the most important IPLs in the water column of the studied area.

In summary, I strongly feel that this manuscript still needs quite some revision.

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ED: Reconsider after major revisions (16 Aug 2018) by Markus Kienast

AR by Florence Schubotz on behalf of the Authors (27 Aug 2018) Author's response Manuscript

ED: Referee Nomination & Report Request started (28 Aug 2018) by Markus Kienast

RR by Anonymous Referee #3 (20 Sep 2018)

Suggestions for revision or reasons for rejection

I am happy to note that the authors finally acknowledge in their rebuttal that the extraction technique used is not really appropriate for analyzing intact polar lipids (IPLs) as it may cause changes in the distribution, especially with respect to the abundance of the relatively labile phospholipids. They now state in their manuscript “Soxhlet extractions, rather than for example microwave assisted Bligh-Dyer extractions, were chosen at the time because it was the only feasible way to handle the double 142mm filters. Extraction protocol surely can affect IPL distributions; as shown by Lengger et al. (2012) for smaller sediment samples.” (lines 196-197). This is a bit weird since the Bligh Dyer extraction technique method was already published in 1959 and it remains unclear why this method could not be used on GFF filters. A quick search reveals that these kind of extractions were already described in 1997 (Macnaughton et al., Journal of Microbiological Methods, 31 19-27) so “at that time” is inappropriate phrasing. They should also specify what kind of effects this extraction technique has on IPL distributions, specifically on the abundance of phospholipids. The effects of their unconvential extraction method should be taken into account in interpreting the data in the whole manuscript. I still read in the abstract “Abundant non-phosphorus 44 “substitute” lipids within the OMZ suggest that the indigenous microbes might be phosphorus limited (P 45 starved) at ambient phosphate concentrations of 1 to 3.5 µM, although specific microbial sources for many 46 of these lipids still remain unknown.” The authors cannot talk about “abundant” because their extraction method does not allow to say anything about the abundance of one type of IPLs over another type of IPL as their extraction method leads to a bias in the distribution (especially if it relates to phospholipids. If the authors fail to build this concept into their manuscript, it remains flawed.
I welcome the changes that have been made to Figure 4 (representation of minor IPLs) although (as indicated earlier) their extraction technique will have a substantial impact on the relative abundance of the phospholipids. In all tables and figures the authors present in this manuscript they have to mention in the legend or footnote that the extraction technique used has led to a discrimination of the phospholipids. Otherwise, presenting these data is not scientifically correct.
It is also nice that the authors now provide data on the analyses of the mixtures of standards over time (the new. Fig. S1). However, the legend of the figure should explain what is shown in the first panel: is it the response of all IPLs comprising the standard mixture? Furthermore, they should specify the initial composition of the three standard mixtures in much more detail (concentration of the specified IPLs). The authors also report relative abundances of specific IPLs (e.g. GDGTs with a variety of polar head groups) but these IPLs are not represented by any of the IPL standards they use in their Standard Mix. How, are they able to derive mass spectrometric response factors for these IPLs. An explanation is required.

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ED: Reconsider after major revisions (24 Sep 2018) by Markus Kienast

AR by Florence Schubotz on behalf of the Authors (16 Oct 2018) Author's response Manuscript

ED: Publish as is (17 Oct 2018) by Markus Kienast

AR by Florence Schubotz on behalf of the Authors (18 Oct 2018) Manuscript

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Short summary

Organisms living in natural environments have to cope with constantly fluctuating conditions in order to compete and survive. Hereby, membrane lipids may play an integral role. This study demonstrates that the lipid repertoire and lipid modifications in marine picoplankton living in oxygen minimum zones may be larger than previously thought. The abundant presence of non-phosphorus lipids hint at nutrient limitation within deeper depths of the ocean, even though these are not considered as such.