Review of Saavedra-Pellitero et al._submitted to EGUSphere.

Title: “Pacific Southern Ocean coccolithophore-derived particulate inorganic carbon (PIC): A novel comparative analysis of in-situ and satellite-derived measurements”

Summary evaluation and general comments

I think the study is valuable and, after some major revision, should be published.  One overall issue is with the way they focus the study in the Title, Abstract and Intro goes into the weakest result where they do not succeed in resolving things so well.  They clearly consider the greatest importance to be the comparison of the in-situ and satellite data, but I think they end up raising more questions in this sense than they succeed in resolving.  A major deficiency is the lack of direct discrete measures of PIC by chemical analysis with to which to compare microscopy-based and satellite estimates of PIC. Without such data, they really can’t complete a proper comparison. I recognize that it is not always trivial to get or process such samples, and I see some other points of value. The strongest findings are that a) coccolithophores are not contributing significantly to the apparent high PIC estimated by satellite in the Antarctic Zone, but are important further north; b) they strengthen what we know of the biogeographic patterns in the high latitude southern hemisphere, picking two very important but quite distinct part of the circumpolar circulation; c) there are uncertainties and disagreements between methods for estimating coccolith-PIC using SEM and or polarized microscopy and they provide information that allows evaluating that disagreement.

The first of those three points, that the AZ satellite signal assigned to PIC is not from coccolithophores, is both one of the most important results, but it is also the only part where they do a strong comparison between satellite and microscope-based approaches. In the rest, they do not complete the comparative analysis with a statistical comparison of the different approaches.

Consequently, my recommendation is that the authors should be encouraged to submit a major revision, and I suggest to them to change their focus to the points where they generate robust results that are nevertheless valuable.

Major specific comments:

Lines 101-106 and later (generally). This study seems to combine previously published data with new analysis, specifically with new analysis that relies on samples which were analyzed more deeply.  It would help to cite that or those previous studies from these transects in this paragraph.  I think early in the Methods there should be a first table defining where the samples come from, including noting in which previous studies they have been used in.

Lines 191-206: 3.3 Satellite-derived PIC data

I think it is interesting to compare in situ data to the output distributed from the NASA group, but then I am not sure what exactly they did.  Did they compare a single pixel to each discrete sampling?  Beyond showing later that there is a region of very high satellite signal with low or absent coccolithophores, I suspect this sampling is not really sufficient to do a true comparison of the satellite vs discrete measures.

Section 4.1.

Lines 233-237: “Weekly and monthly MODIS-derived PIC at the sampling locations consistently overestimate PIC values… with respect to in-situ values calculated from coccolith mass” and “there is a relatively good agreement in the latitudinal satellite and coccolith-PIC trends in the SAZ and PFZ”  and again at lines 292-293: “In the studied transects, the calculated coccolith-PIC and the satellite-derived PIC trends show quite good agreement in the SAZ and PFZ,”

This is a possibly highly subjective, evaluation of correspondence has been made.  What is “good agreement”?  Sometimes when coccolith-estimated PIC is low, satellite-estimated PIC is also low, and when coccolith-estimated PIC is higher, satellite-estimated PIC is also higher, but, even in the SAZ and PFZ they do not track precisely.  I do not think they could track precisely even if all PIC was from coccoliths and the estimations were completely faithful, because one is a very discreet estimate at a single sample in a single Niskin bottle, and the satellite value is an average over at least many days.  So they can’t correlate perfectly.  Nevertheless, to make the statement it would be nice to see a direct analysis of the correlation between coccolith-PIC (calculated) and satellite-estimated PIC. That is, I’d like to see figure, combining both datasets, plotting one against the other.

Also, the phrasing could be more careful in lines 233-244, because “consistently overestimate PIC values” is only correct if one knows that most PIC comes from coccolithophores instead of other sources, which might not be true. Also, it is not clear if there is a way of knowing the error on the coccolithophore PIC estimation.

There are several reasons why the estimates could not agree.  Here are just some principal possibilities:

• Perhaps the satellite estimates in fact are right, but a lot of coccolith PIC is in the form of coccolith fragments that are too fragmented to be recognized and counted, so microscopy estimates would be lower than the “true” value
• Perhaps there is another PIC producer (although that possibility was implicitly considered in the Intro)
• Perhaps the assumptions in the coccolith-PIC calculations are actually wrong (e.g., the shape factor is different than estimated, or the number of coccoliths per cell assumed is wearing)

In the Discussion, the authors do touch on some of these and other possibilities, but I would like to suggest they might try a modest reorganization so as to make it clear to go one by one through the possibilities to consider.

Line 270: “The relative tube width’ (an index for calcification; Young et al., 2014), calculated using equation 2, varies from…” 

How do you deal with the issue that the “overcalcification” is variable?  The tube width in the “overcalcified” forms tends to be very irregular, and sometimes the central area is covered nearly fully. This should be made explicit, perhaps with a new panel in Fig. 2 or a supplementary figure associated with the Methods section to show how this complicated situation (like the case in Fig. 6 bottom left) is dealt with.

I have some concerns about the PCA and how it is discussed.

First, the PCA does not seem to be very successful at separating the coccoliths based on morphometric parameters.  Except for the overcalcified forms, which separate only based on tube width (needs to be clearer how that is really measured, as discussed above), the other forms overlap a lot.  In fact, component 2 in the PCA, which correlates mostly with other morphometric characters quantified, does not appear to separate the morphotypes at all.

Some of the characters that have been used for separating types A and B are not analyzed, and might be quite difficult to analyze automatically (such as central area type, or whether the distal shield elements or straight or not). I think it is definitely valid to do and report the PCA, but it is important to discuss the fact that this analysis, using the current state-of-the-art quantification, seems to fail at what are visually quite striking differences is very notable.  This suggests that perhaps it is time to try new approaches to distinguishing these types.

Second, the issue also makes me wonder if we have independent estimates of how well the approaches of trying to estimate coccolith PIC by morphometry or by polarized microscopy work when comparing different morphotypes.  It seems that, while there are many studies that directly quantity PIC in culture (either as acid-labile particulate carbon or as particulate calcium), it is hard to find any that also count the number of coccoliths to measure PIC/coccolith. It might be worth highlighting this need. I should mention, and not parenthetically, that I appreciated a lot the analysis they showed in Fig. 8, which goes directly to this point.  I think their data suggests we are still lacking precision in the way we measure coccolith PIC, and I would hope that, while their study might not resolve it, at least it helps identify the problem.

Third, in lines 346-347 they say: “The PCA performed on the E. huxleyi morphometric dataset shows that those heavily calcified type A coccospheres occupy a relatively restricted ecological niche offshore of Chile” The PCA is only based on morphometric characters, regardless of the location or oceanographic conditions in which they are found. How can such a PCA, which does not include any environmental information, indicate anything about whether the ecological niche of one form is restricted or not?

For Figure 1, and the corresponding description in the Methods (lines 108-122), I could not tell if the white lines correspond to average positions of the fronts or to the positions the fronts occupied at the time of the study.

Minor technical and comments and corrections

Abstract: Eliminate page breaks within abstract

Line 84: Perhaps reserve “concentration” for chemicals (such as PIC) and “abundance” for cell or coccolith numbers/volume.  It’s not strictly necessary, but it might help to be clearer

Line 88-89 : “ available coccolithophore concentrations” maybe clearer “available measurements of coccolithophore abundances”

Line 98: “have targeted areas of coccolithophore bloom”.  Should be “blooms” (plural)

172-173: “and modified for E. huxleyi according to the degree of calcification obtained for each morphotype (see Table 1)”  How is this modification of K_S according to calcification performed?  Is there a reference?

Line 178: “Measurements of the distal shield diameters of Calcidiscus leptoporus the second most abundant species”  Need a comma after “leptoporus”

Line 265-266: “Note that this data is shown in Figures 3 and 4, but the coccolith-PIC was calculated in this work using equation 1 and the average lengths mentioned in Table 1 “  Not clear.

Line 270: We observed that some coccoliths are clearly overcalcified (see Figure 5 for an example),…” Do you mean Fig. 6? Fig. 5 doesn’t have any photos so can’t see that observation.