Dear Author,

Thank you for submitting a revised version of your manuscript submitted to Biogeosciences. I have now read it and decided to send it for a second round of review.

I will let you know the outcome as soon as possible.

Best regards,
Jean-Pierre Gattuso

Dear Author,

Thank you for submitting a reply to the referees' comments as well as a revised manuscript. There remains issues preventing acceptance of your manuscript for publication. I appreciate that you have added suitable caveats and recognized the limitations of your analysis and those in the original data. The fear that readers would blindly accept the pigment interpretation without reasonable understanding of the limitations has therefore been somewhat alleviated by the revised text. However, the list of 'supporting' references is misleading — many cite each other another. Support of the idea that the 19-hex pigment is a direct measure of coccolithophore biomass is not as strong as the manuscript implies. Another issue is the statistical significance as the increase relies on a limited part of the data set.

I am now in receipt of two referees reports (pasted below) which provide more context about the issues above. They also provide specific suggestions that I strongly encourage you to consider. Among them is the title which does not reflect the limitations of the study. This could be dealt with using one of the titles below but feel free to explore other options:

- Apparent increase in coccolithophore abundance in the subtropical North Atlantic from 1990 to 2014
- Increasing coccolithophore abundance in the subtropical North Atlantic from 1990 to 2014?

Figures R1 to R3 are very useful to discuss the limitations. They should be provided as supplementary information so that you can refer to them in the text as needed. Finally, Biogeosciences strongly promotes the full availability of the data sets reported in the papers that it publishes in order to facilitate future data comparison and compilation as well as meta-analysis. This can be achieved by uploading the data sets in an existing database and providing the link(s) in the paper. Alternatively, the data sets can be published, for free, alongside the paper as supplementary information. The ascii (or text) format is preferred for data and any format can be handled for movies, animations etc…

Please provide a point-by-point reply to the comments provided in this second round of review. I hope that you will satisfactorily address all issues so that the review process could come to a timely end.

Regards,
Jean-Pierre Gattuso
Editor, Biogeosciences


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Referee #1

The revised paper now incorporates suitable caveats to make it clear the limitations of the inherent assumptions. However, I would like the authors to clear something up: there is a circular argument in some of the references they mention that should be removed or simplified, i.e.

- Lomas and Bates (2004) – This reference does not implicitly prove that haptophytes or 19-hexanoyloxyfucoxanthin (19-hex) are directly related to coccolithophores, rather they reference Haidar and Thierstein (2001) to support this assumption. They state ‘the Haptophyte group includes the coccolithophorids, for example, Emiliania huxleyi, that have been shown to be very important at BATS (H&R 2001)’ and ‘it is known that the Haptophytes present (at BATS) are dominated by Emiliania huxleyi that is on average >5 μm (H&R, 2001).’ Haidar and Thierstein (2001) never state that E. huxleyi, or the coccolithophores, dominate the haptophytes and make no direct comparison to pigments in this paper - they simply state that E. huxleyi dominates the coccolithophore community.

- Steinberg et al. (2001) – This reference assumes all 19-hex comes from prymnesiophytes and that these are mostly coccolithophores. They provide no direct evidence to support this. Hence, using this reference to support the statement that ‘coccolithophores comprise between 1% and 30% of chlorophyll a in subtropical gyre environments (this study-see Figure 2, Steinberg et al, 2001; Cortes et al., 2001)’ assumes that all the 19-hex comes from coccolithophores. Please also note that Cortes et al. (2001) never looked at pigments in the context of their coccolithophore cell counts and also do not provide data to support this statement. (Also, the ‘under bloom conditions they can approach 100% of the phytoplankton community’ is not true – coccolithophore blooms incorporate many other phytoplankton groups, including diatoms and other flagellates (see e.g., Fernandez et al. 1993; Balch et al., 2014).

- Dandonneau et al. (2006) – Show a very poor relationship (their Figure 14) of 19-hex and coccolithophore biovolume (in fact the abstract states this), with the relationship mostly being driven by their data from the Pacific North Equatorial Countercurrent (PNEC); their data in the South Pacific Subtropical Gyre shows no relationship when examined alone (see their Fig. 14).

- Kavanaugh et al. (2014) – State ‘We acknowledge the debate regarding the common usage of 19-hex to indicate oceanic coccolithophores because of its occurrence across multiple coccolith- and noncoccolith-forming taxa (Van Lenning et al. 2004). However, recent investigations have found good agreement (?) of 19-hex concentrations with coccolithophore biovolume (Dandonneau et al. 2006). Hence, this assumption is not independent of Dandonneau et al. (2006) and again shows no direct data that supports this assumption.

- Riebesell et al. (2007) – This is based on mesocosms, where they do have pigment and coccolithophore cell counts, but never state in the paper that the two are equal: i.e., they talk about Prymnesiophyte pigments being predominantly from E. huxleyi.

To conclude, the references cited by the authors include many inter-referencing and some incorrect information that should be clarified. None of the ‘numerous studies that agree with the conclusion that haptophytes are mostly coccolithophores’ provide direct data (apart from Dandonneau et al. 2006). The expanded explanation of how the authors have corrected for the different types of haptophyte pigments and the extended section on the limitations of the study are sufficient that readers of the paper do not blindly assume 19-hex is equivalent to coccolithophore biomass – referencing other studies which have done so does not help the argument (or the literature).


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Referee #2

Most of my comments have been adequately addressed by the authors and several aspects like the uncertainties in deriving coccolithophore biomass from pigment data are discussed in more detail.

However, my main concern remains, i.e. there is only a statistically significant increase in Chla_hapto (Fig. 7a) from the early nineties onwards if the time series analysis is ending in 2012. No statistically significant increase is found for any other end year. Furthermore, pronounced (in terms of signal strength) and statistically significant trends, both negative and positive are found on shorter time scales, indicating some sort of cyclicity. This issue together with the uncertainties associated with deriving coccolithophore biomass from pigment data or satellite based particulate inorganic carbon estimates, should be clearly reflected both in the title (maybe consider adding a question mark) and the abstract, but also dicussed further in its overall implications.

Another important aspect here is the observed magnitude of a potential trend. The authors should relate the calculated yearly concentration changes (please check the units in Fig 7a as they seem to be an order of magnitude too high, and also consider using the same units for Figs. 5,6 and 7) with average concentrations. Only then it becomes possible to judge whether an observed change, although potentially statistically significant is actually significant.

The above comments on potential cyclicity versus long term trends and overall magnitude of such potential trend should also find consideration regarding the satellite products presented in figure 8. Furthermore, although the authors state that there is an overall statistically significant correlation of SeaWiFS and MODIS PIC data with Chla_hapto, the increase in latter during the last couple of years, which is actually responsible for the apparent long-term trend from the early nineties until 2012 (but also see comment above), is not at all reflected in the satellite data at BATS (compare Fig. 5). Thus, I do not see how the satellite is backing up the Chla_hapto data.

ADDITIONAL COMMENTS:

1) The Schlueter et al. (2014) paper can not be used as a reference for coccolithophore calcification being insensitive to increasing CO2 in comparison to many other studies. First of all, it is assessing adaptation potential as opposed to physiological acclimation, second, the rates reported there are not directly comparable to other studies as not being the standard amount of calcium carbonate per cell per day, and third, the restoration of calcification rates (integrated over five days) to higher than present day levels was only found in a combined CO2 and warming assay of the high CO2 high temperature acclimated cultures.

2) Concerning the potential DIC limitation of photosynthesis in coccolithophores in the modern ocean, the authors mention a threshold of about 10 μmol/L. Fig. 2 in Riebesell et al. (2004), from which they derived this value, highlights the problem I had with the notion that the change in seawater CO2 during the last 20 years could directly be responsible for changes in coccolithophore abundance by increasing growth rates. As shown in this Fig. 2 the increase in photosynthetic rates when increasing seawater CO2 concentrations from about 10 to 15 μmol/L (equivalent to increasing atmospheric CO2 from a bout 250 to 400μatm which is far greater than what would be expected for the last 20 years) is relatively small, on the order of a few percent. And although there are other physiological studies showing more pronounced decreases in photosynthesis below 10 μmol/L of CO2, the CO2 increase during the last 20 years would be bound to minimal changes in photosynthesis.

3) The explanation for an opposing pattern in Synechococcus and Haptophyte abundances described in the paper (Synechococcus is driving Haptophytes into DIC limitation) is not convincing. If photosynthesis by other autotrophs would actually be able to provoke carbon limitation in haptophytes why then is there only a opposing pattern with Synechococcus? And secondly, it is again about the magnitude of a response. Both papers cited by the authors (Riebesell et al. 2004 and Rost et al. 2003) show a very small response in photosynthesis for reasonable (on the order of a few μmol/L) CO2 changes, expected for the open ocean.

Dear Author,

Thank you for submitting a revised version of your manuscript submitted to Biogeosciences, which I am glad to accept for publication.

Note that I did not request that you archive the data with Biogeosciences. I did mention the fact that links to data archived elsewhere were fine. Please provide these links in the methods section rather than in the acknowledgement section. Are the data for Fig. S3 also available somewhere? If they are, please also provide the link. If not, they should be submitted with the final version of the manuscript.

I look forward to seeing this paper published and thank you for considering Biogeosciences to publish these results.

Best regards,
Jean-Pierre Gattuso
BG Editor