|This is a very much improved version of the original manuscript. I would like to congratulate the authors for the efforts carried out, which have led to this much clearer version. I value very much their data representation and analysis, particularly the inverse model analysis.|
Reading this improved version, two main ideas come to my mind, which I point next. I also enclose the pdf file with a number of editing comments and suggestions.
(1) The authors state that their inverse model does not include diapycnal mixing. The authors argue that this is not necessary as the overall mass balance is good and the imbalances for individual layers are not very large. The largest imbalances occur in the surface waters (SW; -0.66 Sv) and central waters (CW; 0.60 Sv), although these values are less than the calculated uncertainties (0.9 and 2.0 Sv, respectively) (Table A2). They ascribe these imbalances to the role of mesoscale eddies that are not properly sampled.
However, in my view, the data suggest something different. The 0.66 Sv gain in the SW fits fairly well with the loss of 0.6 Sv in the CW. In contrast, the intermediate waters (IW) only experience a loss of 0.03 Sv. The implication to me is that there are about 0.6 Sv of water upwelling in the coastal zone.
Considering a coastal upwelling region 600 km and 100 km wide, the imbalance of 0.6 Sv would represent an upwelling (actual transformation of CW into SW) at a mean rate of 10 m/day over the entire region, which is very reasonable.
In table A3, the authors provide additional information on the CW imbalance split into the subtropical and tropical domains. They find that most of the imbalance takes place in the subtropics (0.48 Sv as compared with 0.12 Sv in the tropics). This is again consistent with our knowledge that upwelling off NW Africa is higher in the subtropical than in the tropical waters.
One possible way to corroborate these ideas is by repeating the inverse model analysis but closing the box with the eastern section rather than with the coastline. If the above argument is correct, you will find that the imbalances in the SW and CW layers decrease substantially.
(2) The mass and property imbalances in the CW and SW are used to draw conclusions about net primary production in SW and net remineralization in CW. This is a very important result, probably among the most important ones in the manuscript. However, the high water mass imbalances in the SW and CW leaves the reader thinking how much of the oxygen and inorganic nutrients imbalances are related to physics (water-mass imbalance) and how much is related to biogeochemical processes (mostly primary production and remineralization). This is particularly troublesome as some of the imbalances have uncertainties that are larger than the estimated values.
I believe that the inverse model analysis should be carried out again considering the point (1) above. You can do something simple such as setting the imbalance in the SW as and additional water-mass transfer from the CW to the SW (upwelling transfer). You will likely find that the physics of the model does much better, even with lower a priori uncertainties so that your error bars are smaller. This is essentially equivalent to having 0.6 Sv of CW (and associated biogeochemical properties) being transferred from the central to the surface layers. In my opinion, only after you do this is that your results will be meaningful.
One additional step forward would be to split this upwelling transfer among the subtropical (0.48 Sv) and tropical (0.12 Sv) domains. In this way you will be able to discuss your results in terms of what happens in the subtropics and what happens in the tropics. For example, I would expect that primary production and remineralization is much greater in the tropics than in the subtropical but right now you are finding precisely the opposite.
Some additional minor comments and suggestions:
(3) In the enclosed pdf I suggest some modifications for the abstract, plus a number of editing suggestions.
(4) p. 5, l. 5: “to validate the temperature interpolated to the XBT positions and set the signal to noise ratio...” I agree with the signal-to-noise ratio but you do not use interpolations to validate a measurement but the other way round.
(5) p. 5, l. 8: 10%? Is this correct, 10% and even 5% is far too high: 5% of 20C is 1C, which is very large.
(6) p. 5, l. 13-14, please clarify.
(7) p. 6, l. 20: I’m not sure about how the journal handles citations to manuscripts in preparation but I would say this is highly irregular. I suggest simply to state “(not shown)”.
(8) p. 7, l. 2-3: “to avoid any issues related with the temporal evolution of structures, the volume is closed with land instead of with the eastern transect”. Please clarify.
(9) p. 9, l. 27: explain this beforehand, in section 2.2.
(10) p. 10, l. 14-15 and elsewhere (including tables): I suggest not mentioning the results for DW. You are only sampling a tiny fraction of these DWs, what is the sense of providing these values?
(11) P. 12, l. 12: Luyten et al. (1983) did not document this shadow zone, they provided a theory that explains its existence. You may rather for example cite Kawase and Sarmiento (JGR, 1985).
(12) Fig. A1: I suggest you show the grid every 1 degree.
(13) Fig. A11a: I suggest to separate SW from CW and remove the DW results.
(14) Fig. A15: perhaps you are missing an axis for phosphate transports?
(15) I suggest adding an additional figure like A15 but for the net values, both within the original domain and within the domain that excludes the upwelling region.