In this work, Cantarero et al. investigated the lipid remodeling in phytoplankton in response to various environmental variables by mesocosm experiments, including oxygen concentration, temperature, pH, nutrient concentration, chl-a, and light availability. By combining multiple linear regression and random forest model, the main and secondary factors affecting lipid category and lipid distribution were identified. In general, the presented results are interpreted by suitable assessment methods and the novel and important conclusions are supported by the data. In addition, the paper is very well written and fits in quite well with the theme of this special issue, I recommend the manuscript for publication after the following several problems are addressed.

General comments

• What substances can be called intact polar lipids, it is best to give some examples in the introduction section, and contain specific standardized definitions.
• Page 4, Line 36: What is the specific sampling depth of the surface and subsurface layers, and what is the difference between them? There doesn't seem to be an obvious definition.
• How efficient is it to use the lipid extraction method described by the author, and has the author conducted relevant validation? Moreover, the analysis conditions of mass spectrometry need to be mentioned appropriately briefly in the methods section, rather than directly citing the literature. What was the detection limit for the various lipids in this study?
• Since I am not an expert in this area, I would like to ask whether the sample number requirements of random forest can be met in this study, and how many sample number were used to conduct it?
• Authors would be well advised to standardise the format of journals for references, mostly abbreviations but also full names, e.g. Nature Communications. Please check the format of references in the manuscript.
• Figure 2C: This figure lacks the axis title of the right Y-axis, which is the total chl-a concentrations in µg/L.

Minor comments

• Page 3, Line 91: Please check this sentence.
• Page 6, Line 78-84: Dichloromethane:Methanol:Phosphate buffer, Dichloromethane / Methanol / Trichloroacetic acid buffer, it is better to unify the two forms. N2 required subscript.
• Page 7, Line 11: n = 34in total, lack of space.
• Page 22, Line 88: This sentence lacks a full stop. Line 13: 2m and 17m, lack of space.
• Figure 8A: Check R² in the diagram.

Review of the manuscript egusphere-2023-3110: „Lipid remodeling in phytoplankton exposed to multi-environmental drivers in a mesocosm experiment“ by Cantarero et al.

Using samples from the eastern tropical South Pacific off the coast of Callao, Perú, the authors investigated the lipid remodelling of phytoplankton in the mesocosm in response to various environmental stressors

I have a big complaint about the authors constantly talking about TAGs in the discussion in almost all the subsections, even though they have not analysed them. Especially in the Abstract, the authors go too much into the redistribution of IPL to TAG production in response to various stressors. I think this is unacceptable, especially for the Abstract.

I found the manuscript exhausting to read. There are too many unnecessary discussions.

I suggest that the authors use the common abbreviations for mono- and di-galactosyldiacylglyercols and sulfoquinovosyldiacylglycerol, namely MGDG, DGDG and SQDG.

There is unnecessary over citations in the manuscript. The authors have cited 3 or more articles for one statement, one or two would be enough. Consequently, there are too many references (157).

The first digit of the three-digit line numbers is not visible. I hope I have estimated the line number correctly in the comments.

In accordance with the above and the specific comments below, I suggest that the manuscript can be published after Major revision

Abstract

L 45 – cellular P as well

1 Introduction

L 49-50 – In general, three citations are unnecessary. E.g. Ulloa and Pantoja, 2009 and Thamdrup et al., 2012) would be more than enough. This comment applies to all cases where there are 3 or more citations for a statement.

L 72 – The citation Catalanotti et al. (2013) is inadequate and should be removed.

L 79 – All the cell organelles have lipid membrane!

L 80 – I do not find citations Du and Benning 2016; Morales et al., 2021 appropriate.

L 81 – The citations Urzica et al., 2013 and Gordillo et al., 1998 are missing in the References. I suggest to remove it due to the over citations.

L 82 - Sato et al., 1979 or 1980? Also, the citations Wada and Murata, 1990 and Sinensky, 1974; and Tatsusawa and Takizawa 1996 (first time mentioned) are not appropriate and should be removed.

L 84-85 - The citation Gombos et al., 2002; Pineau et al., 2004; Simionato et al., 2013; Gašparović et al., are not appropriate and should be removed.

L 91 - community level and in time series, s, and the associated

2 Methods

L 123-124 - It is not clear on which day the ODL water was added. Days 5 and 10?

L 176 – I did not find the protocol for lipid extraction in the paper by Wormer et al. (2013). Therefore, this citation is inadequate.

3 Results

L 285, 314, 325, 330, 347, 354, 369, 373, 377, 379 – It would be easier for me to follow the text and Figure 2 if the mesocosms were listed in the order shown in Figure 2. E.g. to say in line 325: ... mesocosms 7, 5 and 8.

L 301-302- Fig. 2: The concentrations of the nitrogen species ranged from less than 1 umol/L. The Si concentration in Table 1 is also high (> 17 umol/L), whereas it is not shown in Fig. 2. Is this a question of dilution?

L 417 – I am not familiar with Card and Random Forest. Perhaps it would be good to include in the Supplements an introduction to understanding Figures 4-7.

My biggest problem is understanding where in Figures 4-7 there is confirmation of what some authors say. I would like an answer to this:

• How can I see that Oxygen concentration was important in predicting MGDSs in Fig. 4E and F?
• How can I see that Oxygen concentration was important in predicting DGDSs in Fig. 5A and B?
• How can I see that temperatue was important in predicting PE predictions in Figs. 6E-H?
• How can I see that Various forms of biologically available nitrogen were important in predicting MGDS in Fig. 4E?
• How can I see that NH4 was important in predicting BLs in Fig. 5E?
• How can I see that NH4 was important in predicting PEs in Fig. 6E-H?
• How can I see that PO4 was important in predicting SQDGs in Fig. 4A?
• How can I see that PO4 was important in predicting MGDGs in Fig. 4E?
• How can I see that light availability was important in predicting SQDGs in Fig. 4A?
• How can I see that light availability was important in predicting MGDGs in Fig. 4E?
• How can I see that light availability was important in predicting PEs in Fig. 6E-H?
• How can I see that light availability was important in predicting PCs in Fig. 7A?

4 Discussion

L 563 – only Fig. 3

L 563-565 – I do not understand this sentence. First the authors state that there is more unsaturated IPL at lower pH values (i.e. in the subsurface), then they state that this is most clearly observed in surface waters???

L 573-574 – pCO2 is not concentration but the partial pressure of CO2.

L 579 - Hu and Gao et al., 2004 ???

L 581-618 – The authors have devoted 4 paragraphs to the discussion of the TAG synthesis. I agree that it's fine to assume that TAG accumulates under unfavourable conditions, but considering that they did not analyse TAG, I think such a long discussion on TAG is an exaggeration.

L 608-609 – I suggest that the authors consider why dinoflagellates are more dominant in the surface layer. Dinoflagellates are possibly mixotrophic, some are also heterotrophic, while diatoms are probably limited by Si availability.

L 631 – How is 125-220 µmol/L just 28% more than ~15-75 µmol/L?

L 682-683 – Did the authors analysed the influence of temperature on each individual IPL separately?

4.2.5 Light Availability - Considering that the mesocosms had low light conditions and not high light conditions, I think it is unnecessary to discuss other works about high light conditions.

L 740 - 741 – The authors should read more recent works on the role of SQDG, e.g. DOI: 10.1042/BCJ20170047 ; DOI: 10.1074/jbc.RA118.004304

L 766-767 – I assume it should be written: ... LOW light availability may amplify the effects of other environmental stressors...

L 783 - 4.3.1 Relative adaptability of Phytoplankton Classes to environmental change: Most of the text in this subsection, including Fig. 8, should be moved to the Results section.

Figures

Fig. 2c – The legend of this fihure lacks an explanation for the black line (chl a).

I suggest to change Chl-a y-axe from 0-10.

Fig. 2d – it would be better to organise the IPLs according to their cellular origin. I would suggest the following order: MGDG, DGDG, SQDG, PG, PC, PE, BL and others.

References

In some references the name of the journal is written with the full name, in others with an abbreviation.

The reference Jiang and Jónasdóttir should be separated from the reference Hutchins and Jiang

Reference Guckert, J. B., and Cooksey, K.E.: to correct: …high Ph‐induced... DOI: 10.1111/j.0022-3646.1990.00072.x

Reference Schubotz, F., Xie, S., Lipp, J. S., Hinrichs, K. and Wakeham, S. G.: is poorly written.

Also, The reference “Schubotz, F., Xie, S., Lipp, J. S., Hinrichs, K. and Wakeham, S. G” should be separated from the reference Shulz and Riebessel

Reference Cantarero should be improved: ... Front. Mar. Sci. 7:540643. doi: 10.3389/fmars.2020.540643, 2020...

Cantarero Biogeosciences Notes

Summary:

The authors use a combination of multiple linear regression, random forest algorithms, and classification trees to interrogate how physicochemical environmental factors and phytoplankton community structure drive the bulk intact polar lipid pool.

The authors have combined an impressive array of approaches to tease apart a complex system, and the application of these methods to environmental lipidomics is relatively novel (though this paper makes its difficulties clear). Models like these are an important aspect of how the field is currently thinking about interacting environmental drivers, and, with some work, this paper could shed light on how these variables influence the community lipidome and how the lipidome may influence community structure. The paper was generally well written, though the discussion was overly-long and I often felt like it lacked direction, so I would recommend reducing the amount of speculation in the discussion, especially with regards to unsubstantiable TAG production. 

These are the areas where I think the paper could be significantly improved:

In the MLR section, the authors performed 1650 statistical tests (10 parameters x 165 IPLs), the results of which drove a significant portion of the discussion, but they did not mention controlling for false discovery rate. Additionally, the authors mentioned many IPL classes showed both positive and negative relationships (e.g. SQDG), confounding deep interpretation and leading to an extremely long discussion with many “possible explanations.” Controlling for FDR would likely reduce the number of significant relationships, and may help the authors focus their efforts on more significant and powerful correlations and therefore drivers of IPL abundance.

Due to this lack of clear direction, paragraph and section structure in the discussion was not always clear—by that I mean, frequently, the authors suggest a potential cause of various differential IPL abundances, often with little or no evidence in the data and with a citation of a singly study, and then the idea is dropped after a couple of sentences without a clear tie to an overall narrative. Potential TAG production was often invoked as an explanation, despite no TAG data in the manuscript, and I hesitate to endorse such an overarching conclusion with no evidence to support it.

Additionally, there was little to no mention of bacteria, or of IPL abundance as a proportion of particulate organic matter—I am not an expert in the Peruvian Upwelling Zone, so it may be that they are an insignificant proportion of the biomass in this location. However, many of the IPLs in this study are prevalent in bacteria (e.g. PE, PG, DGTS, MGDG), in some cases moreso than in phytoplankton. (Twice, the authors suggest a higher IPL/chl a ratio in the subsurface is indicative of greater IPL contribution to phytoplankton biomass—however, this could be explained by either non-phytoplankton, i.e. bacterial, or non-living/detrital IPL pools.) This inquiry may help the authors ground their interpretations of the community response to environmental stressors. Without this understanding of how phytoplankton IPLs fit into the total organic carbon pool, many of their interpretations are incomplete.

Finally, throughout the Discussion, the authors suggest potential triggers that induce microbes to alter their IPL pool (e.g. light, pH, temperature, etc). However, the authors then jump to invoking them as the actual cause in the Conclusion, which I do not think is a valid conclusion from correlation analyses—i.e. correlation does not imply causation.

Specific comments

I hesitate to question data, but in Fig. 2D, Subsurface, on Days 12, 16, and 18, PG comprises almost 75% of all IPL’s. I know of no phytoplankton or marine bacteria where PG makes up anywhere near that percentage—I typically think of them on the order of 5-10%, maybe 20%, in phytoplankton (e.g. Cañavate et al. New Phytologist, 2017; Popendorf et al. Org. Geochem. 2011). Anything higher than that would, to me, seem more indicative of marine bacteria, which, as I said, were not mentioned in the manuscript. I would recommend the authors check their quantification calculations.

There are many citations in the manuscript where sources are not listed in the bibliography – e.g. Brandsma et al. 2011 (L 670), Abida et al. 2015, Urzica et al. 2013, Gordillo et al. 1998 (all L 81) – there may be more, but these are the ones I happened to check because I was interested.

L 861 – Where does the 2% N come from? (Citation?)