Validation of Stratification-Driven Phytoplankton Biomass and Nutrient Concentrations in the Northeast Atlantic Ocean as Simulated by EC-Earth

Round 1

Reviewer 1 Report

Overall, I am happy with the revised manuscript. There are a few instances where I think the authors chose the way of least resistance, but after all, it is their paper, not mine.

For future reference, I would like to remark that it is customary to provide a tracked-changes version that also shows what has been deleted, not only what's added/new.

Best,

Achim

Reviewer 2 Report

See the attachment.

Comments for author File: Comments.pdf

This manuscript is a resubmission of an earlier submission. The following is a list of the peer review reports and author responses from that submission.

Round 1

Reviewer 1 Report

Review of "Validation of stratification-driven phytoplankton biomass and nutrient concentrations in the Northeast Atlantic Ocean as simulated by EC-Earth" by Skyllas et al.

Skyllas et al. validated spring/summer phytoplankton dynamics computed in the EC‐Earth‐NEMO earth system model by comparing model results (mixed layer depths, nutrient concentrations, chlorophyll concentrations) with observations from two cruises in the North Atlantic and satellite-derived chlorophyll-fluorescence. They conclude that recently suggested improvements in the vertical mixing scheme do indeed lead to a better, even if not perfect, representation of timing and magnitude of the North Atlantic spring bloom.

I feel the presentation of the results and discussion could be improved. The authors often seem to make general but unreferenced statements and it is not always clear if they are based on other published studies or their own results. The figures could also use a bit of synthesis, especially merging observations and model runs 1 and 2 in the same figures for easier comparison. One could also think about using more quantitative indices of model-observations fit such as root-mean-square errors, instead of only comparison of large-scale means. 

Please find more specific comments in the annotated pdf that the authors may wish to consider when revising their manuscript.

One point, albeit very minor, I would like to stress is the following, as it is a very low-hanging fruit for improvements in presentation: Please do not use the rainbow colour scale, it creates fake constrasts in data and is unsuitable for vision impaired (such as colour blind) people. See e.g. here: https://www.climate-lab-book.ac.uk/2014/end-of-the-rainbow/ or browse twitter: https://twitter.com/hashtag/endrainbow?lang=en. I myself am guilty of publishing a few figures using that colour scale and I wish somebody had told me earlier.

On a last note, there seems to be no data accessibility statement for any of the data (except the MERIS data). Similarly, no mention is made about public accessibility of the used computer code.

In the spirit of Open Science, if anybody should wish to publish or otherwise use this review (including my pdf annotations), I hereby release it under the terms of the Creative Commons CC-BY-4.0 license (unless the journal already has a policy for that in which case I would like to be contacted in case of publication).

I hope my comments help the authors and editor.

Comments for author File: Comments.pdf

Reviewer 2 Report

The present manuscript presents a validation exercise of the Earth System Model (ESM) EC‐Earth‐NEMO model outputs (model derived temperature, salinity, phytoplankton chlorophyll a and nutrients) with in situ observations of two cruises in the North Atlantic. This study corroborates the importance of stratification and mixing processes in determining phytoplankton bloom dynamics in the North Atlantic. More specifically, the authors describe how the model deviates strongly in the subpolar North Atlantic due to potential unrealistic high fresh water inflow from the Arctic, failing to accurately simulate mixed layer depth in spring and resulting in unrealistic phytoplankton bloom phenology and magnitude. I think that the subject of the paper is relevant, it is well-written and structured and recommend it for publication. However, the conclusions claimed by the authors need to be backed by further evidence. To be published, I would recommend moderate changes to be done. I have some constructive comments/feedbacks which I hope they help to improve the manuscript.

General comments:

1- Monthly satellite data and monthly averages of surface salinity, temperature, potential density, Chl a, and nitrate concentrations of NEMO/PISCES v2 are evaluated against observations taken on specific days and specific locations during Stratiphyt cruises in summer 2009 and  spring 2011. It is not completely clearly explained whether what it is used in the manuscript are (1) monthly averages of e.g daily model outputs or (2) the model outputs are monthly averages (monthly frequency is the higher temporal resolution available from NEMO/PICES v2 model outputs). In case the authors are averaging NEMO/PICES model outputs of higher temporal resolution (e.g: weekly, daily), some of the information included in the higher frequency data must be included in the manuscript. The reviewer understand that it is not a trivial task. For the purpose of the present manuscript, including the corresponding standard deviation to the monthly average at each location for each parameter (temperature, salinity, ...) may be enough. It would help to evaluate the origin of the discrepancies between model and observations (e.g. the 0.4-0.5 salinity difference between model and observations south of 46°N is within the standard deviation of modelled salinity fields at these locations). In case the authors are using monthly model outputs but there are higher temporal resolutions available, it would be also necessary to include this information. In case monthly model outputs are the higher temporal resolution available, please indicate it specifically in the manuscript.

2- In section 2.1 (L. 102) it is indicated ‘During each cruise, 32 stations were sampled in the upper 250 m by the RV Pelagia’. If there are available data for each station until 250 m depth, why chlorophyll profiles in Fig. 8a and b are in most cases shallower than 150 m? If casts were done until the depth shown in Fig. 8, MLD estimations shown in Fig. 2a are limited to the maximum depth of the casts. Let's consider that the maximum depth of a cast is 150 m. Then, MLD can only be unambiguously estimated if it is shallower than 150 m (e.g. MLD at 100 m). Otherwise, one can only say that MLD is ≥ 150 m. It can be 150, 300 or 500 m. We simply do not know. In the view of that, are MLD estimations north of 50N in Fig. 2c -which seem to coincide in some cases with the apparent maximum depth of the cast in Fig. 8a- affected by this fact? In relation to that, how observations until 250 m allow the following assertion (L.240): ‘North of 55º N the model showed shallower UCMs in spring (average 107 ± 28 m), contrasting with the observations of a near‐constant Chl a distributed over deep mixed layers (average 305 ± 187 m)’?

3- The smoothed shape of model vertical profiles in Fig. 3 are expected since they are monthly averages, but observations look similar. Are in-situ vertical profiles in Fig. 3 somehow filtered?

4- In section 4, it is indicated (L263) ‘Model run 1 showed a low salinity anomaly in the upper 200m, which was most pronounced in the subpolar North Atlantic (55‐62º N). … Model run 1 salinity deviations were also observed during previous validation efforts of the EC‐Earth model (https://dev.ec‐earth.org) that used CORE forcing compared to DFS5.4 forcing that was used in our calculations, and in the interactively coupled ocean‐atmosphere GCM from EC‐Earth. These coincided with an absence of wintertime deep convection in the Labrador Sea, weak Atlantic meridional overturning circulation (AMOC) of less than 10 Sv, and too shallow mixed layers over vast regions of the North Atlantic.’ It would be necessary here to provide further evidence that the low salinity anomaly reproduced by the model in the subpolar North Atlantic is really restricted to the years of comparison 2009 and 2010, and it is not a systematic deviation present every year. It could be done through (1) an additional salinity section for any other selected year by the authors; (2) indicating the salinity differences between model and observations in the subpolar North Atlantic (55‐62º N) for all years except 2009 and 2010 (is it this difference e.g 0.2 instead of 0.7?)

Specific comments:

L 56-58. The writing here seems to link the formation of DCM to permanently stratified regions. As nicely revised by Cullen et al 2015, DCM formation is observable in all waters that remain stable long enough for its development of a DCM (e.g mid-latitudes areas which are not permanently stratified). The reviewer would suggest changing these sentences accordingly.

Cullen, J.J. Subsurface chlorophyll maximum layers: Enduring enigma or mystery solved? Annu. Rev. Mar. Sci. 2015, 7, 207–239

L83-L98. Are not part of these sentences part of section 2 (Methods)?

L 173. ‘The depth profiles of measured … ‘. Are these vertical profiles?

L176. Give here the estimation south of 50°N in line with estimations in L196 or change the estimations in line 196 to south of 46°N as in L176 in the text (see next comment)

L196-198. It would be useful here to give an estimate of how much run 2 reduces the salinity difference between model and observations (e.g: ‘South of 50°N salinity increased by 0.3 ± 0.03, reducing the difference between model and observations in x % (x between run 1 and observations and 0.3 between run2 and observations) ‘ and idem for observations north of 50°N)

L 212. Add latitude range of stations in Fig. 5

Fig. 6. The difference in nitrate concentration between model and observations during spring 2009 are really high. It would be useful to add an estimation of how much would be the nitrate concentrations in the model if MLD were equal to observations (that means which are the nitrate concentrations in the model at the depth of observed MLDs) and how deep should be the MLD in the model to reach the observed nitrate concentrations during spring 2009 (at which depth nitrate concentrations in the model equal that found at the surface from in-situ observations). If the above mentioned problem regarding MLD estimations exist (see general comment 2), it would be also interesting to know at which depth from climatological data nitrate concentration equal that observed at the surface. It could be that MLD were significantly larger than estimated if vertical profiles have been limited to 150-250 m in the subpolar North Atlantic, and it could explained the large difference in nitrate concentrations between model and observations. On the other hand, if an abnormally high fresh water flux from the Arctic is responsible for the low salinity anomaly in the subpolar North Atlantic in the model, couldn’t it also partly explain the differences since Arctic fresh water has different nutrient composition? Previously, as mentioned above, it would be necessary to discard that the salinity difference in the subpolar North Atlantic between model and observations is not a systematic deviation.  All these points should be included in the discussion.

L 266. Consider reordering due to the cause-effect logical order. ‘This salinity anomaly influenced mixed layer depths during winter and early spring, with subsequent effects on nutrient concentrations. As a consequence, run 1 systematically underestimated springtime nitrate concentrations and surface Chl a in comparison to both cruises and remote sensing observations.’

Comments for author File: Comments.pdf