|Evaluation of Busch et al: On giant shoulders: How a seamount affects the microbial community composition of seawater and sponges (bg-2020-15-manuscript-version3).|
The authors improved the manuscript considerably, and the new figures are a welcome addition that make the text better comprehensible. But still, there are a couple of issues left, and the authors' rebuttal to the original comments are not always convincing. Particularly, missing information regarding methodological aspects and a discussion which considers only part of the results make a further revision necessary. I will try to explain my concerns in detail below.
(line numbers apply to the Response to Reviewer Comments in bg-2020-15-AC2-supplement.pdf).
L45: I am not sure about the policy of Biogeosciences, but I think this map is basic information that belongs into the paper proper, not into a supplement
L64: This is not sufficient. As a reviewer of the paper, but also as a reader I do not want (and usually do not have the time) to delve into any data repositories to search for information which is essential for the interpretation of the data, and I see no reason why the authors do not provide this information here.
L69: see comment above. And the information that seawater and sponges were sampled in close vicinity should be provided in the Methods section - this would be just one additional sentence.
L111 ff: I am still not happy with these extrapolations. It is far from clear which parameters go into this "machine-learning process". For example, how were (isolated) BW1 regions outside the data points discriminated from BW2 in the same area - just from depth, which is the only parameter available outside the sampling points? This extrapolation is particularly strange since only one BW1 data point exists, and a possible Taylor column which may be responsible for the BW1 cluster, is locally restricted. Currently, it is kind of a magic black box - something goes in (but the reader does not know what) and the predictions come out. Certainly it is not necessary to go into details, but some basic information of what's going on in the black box would be very useful. And the purpose of the extrapolations/predictions is still not clear: For the outcome of the study, they are not necessary, and they are in fact not used and interpreted in the paper.
L126: I fully agree that Fig. 3 provides a very good conceptual model of how the various parameters around Schulz Bank may interact. But I still feel that this figure does not belong into the results section, because it does not present results, which have not been shown before. In the text of the results section Fig. 3 is mentioned only in connection with the temperature profiles (which obviously are not own results and are hardly discernible in the figure), and that these determine the water mass distribution. Because the limits of the water masses are not indicated, even this information cannot be deduced from the figure.
Nethertheless, the figure is certainly useful for the interpretation of the results, and as such it is in fact used in the Discussion, where it should be placed.
L150: This has to be clarified. According to M&M, 19 stations were sampled, and exactly these 19 stations show up as dots in Fig. 2B, one of which is labelled BW1. Have there multiple (independent) microbial samples been taken per station? This is not mentioned in M&M, but is important information.
L163: I am sorry if the authors feel that my comment criticises their sampling design. I am fully aware of the limitations of deep-sea sampling, and I acknowledge that the authors collected an impressive dataset. My comment aimed at the incomplete information provided in the text - one example is shown in the comment above.
L204: Again, I do not deny the value of the study, on the contrary. But, just looking at the data, some patterns are quite striking, and even if they cannot be tested statistically, they may be relevant and should be considered, e.g. the relative abundances in BW1 being very different from the other clusters.
L214 (and elsewhere in the text and figures): the F value in ANOVA is a ratio, and hence the dF comprise two values.
L240: It is fully ok to discuss the presented data, but since the stations are not directly comparable due to the different distances between near-bottom and water column samples, some cautious statement about the limitations of the conclusion would be appropriate
L244: I do not know where this knowledge comes from, but it is simply wrong. Given the same driving forces, anticyclonic Taylor caps/columns are generated also at seamounts in the southern hemisphere, but of course in counter-clockwise direction (anticyclonic = clockwise in northern hemisphere, counter-clockwise in southern hemisphere). Examples can be found, for instance, in Rogers et al. 2017, Pelagic communities of the South West Indian Ocean seamounts: R/V Dr Fridtjof Nansen Cruise 2009-410, DSR II Vol. 136
L293: I cannot follow this argumentation ("… would enormously inflate the discussion"), and I find it strange to leave the interpretation of results to the reader. If results of the other clades and sponges do not add to the discussion or are not relevant, they can be omitted. The authors now state that Chloroflexi in G. hentscheli are discussed as "representative example". For what is this example representative? Does it mean that the results are similar in the other phyla and clades? Then this has to be stated. But looking at the results, this is certainly not the case.
L324: see also my comment to L64 - the sampling design in relation to the three cruises is not comprehensible from the information given in the paper, and searching in Pangaea is not a reasonable option. And I still miss some convincing statement why interannual variability is no issue.
L330: This is exactly the point. If an influence (of biogeochemical factors) is suggested, the underlying assumption is a causal relationship, which my comment pointed at.