The article presents a model reconstruction of the Arctic Ocean structure during the winter period of the MOSAiC Expedition. The authors used the FESOM2 model with an altered turbulence closure scheme at high resolution. The model results were nudged using profile measurements from buoys, and evaluated against an independent set of profile measurements. The resulting model simulation shows signs of enhanced eddy kinetic energy around the halocline and the depth of the warm Atlantic Water.

While the method seems by-and-large reasonable, in my opinion additional work needs to be done in the analysis and the description of the work in order for it to be ready for publication. A few general comments:

• The authors should clarify the language used throughout. While the methods describing nudging the model using the data, the phrase “nudging of the data” is frequently used, implying that the data where being altered by the model. This should be clarified.
• In its current form, the introduction reads like a list of relevant papers. The paper would be strengthened by integrating the results of prior work into a description of the state of the science for the relevant processes, instead.
• The authors find that there are discontinuities introduced by locations where the trajectories of the buoys form loops. In my mind, this indicates that the ocean is evolving and that treating the observations as a frozen-in-time snapshot is a problem. Perhaps it makes sense at certain time scales and for certain depths.
• The colormaps used in Figure 9 and 7 should be replaced with colorblind-friendly and print-safe colors.
• Minor grammar and typography errors throughout, some are listed below.

More importantly, it’s not clear to me what the key contribution of the paper is. This is not to say the work isn’t valuable or worthy of publication. Rather, I think that substantial revision of the introduction, discussion, and summary is needed to clarify the importance of the work. Clearly a lot of thought and effort have gone into this, and I think restructuring the presentation can bring the value of the work more clearly into focus.

A few (non-exhaustive) minor comments:

6 “drift speed direction” = “drift speed and direction”?

13 “And no” -> “Simulations show no…” or something like that?

18 capitalization unnecessary for “earth system models”

21 Grammar unclear

31 Grammar

75 “so-called” implies that there is some doubt in the name. The site is called Ocean City

80 Define “DN”

85 “one possible method are” grammer incorrect, could replace with e.g. “one possible approach is to use interpolation techniques”

191 DN buoys trajectories -> “DN buoy trajectories” or “trajectories of the DN buoys”

193-4 “these interlacement” unusual word choice, I’d rephrase for clarity

195-196 – Why would we expect the measurements to be the same after a repeat visit? I don’t understand why this would lead to aliasing of a signal.

203 (and throughout, including in the summary). “Nudging of the data” implies that you are altering the data. Is it not the case that you are nudging the model using the data?

400 – What is meant by “or October 2019 to January 2020” here?

A review of "Dynamical reconstruction of the upper-ocean state in the Central Arctic during the winter period of

the MOSAiC Expedition" by Kuznetsov and co-authors. 

My background in is modeling and data assimilation of the Arctic Ocean, but not so much sub-mesoscale oceanography. 

The manuscript exploits a very dense measurement campaign from the ambitious MOSAiC ice camp somewhere in the central Arctic and assimilates it into a numerical model of very high resolution. As there is no other realistic ocean model of similar resolution set up in the central Arctic to my knowledge, the study stands out by its very high originality. 

The closest relatives of such studies were the pioneering ocean forecasts by the Harvard Group in the early 90's where cruise data were assimilated by Optimal Interpolation and fed into a forecast model running onboard during the cruise (Robinson et al. 1996), which did demonstrate forecasting skills. The MOSAiC was however on a slower path at the speed of the sea ice drift and was not in control of the trajectory, so the ambitions stay realistically on a lower level, that of performing an oceanographic process study, which is interesting in its own right. 

The authors did interpolate the temperature and salinity profiles obtained along the whole 4-months experimental period into 3D fields and assimilated these data into a bespoke model set up specifically for the area of the experiment, and then discuss the dynamical features of the simulated ocean fields. 

A major assumption of the study is therefore the synoptic nature of the measurements assimilated ("quasi-steady-state" is not mentioned until line 203 in the methods description, which is very late for an important assumption).  Further on, the model results reveal that this assumption was actually wrong, as acknowledged in the conclusion.  This is a major weakness of the study that should be recognised from the start to avoid some unnecessary suspense. 

Another major weakness is the odd choice of the interpolation method. The inverse distance method is not able to de-cluster observations in an irregular network such as the ones obtained here during a nearly random drift, and generates very erratic extrapolation features, so it should not be used other than with regularly spaced measurements. It is possible that the inverse distance worked well when combined with a clustering method briefly referred to, but it is a priori an ill-informed choice (See Zimmermann et al. 1999 for a thorough comparison, as well as modern examples of interpolation with Bourgain and Gascard 2011 and Troupin et al. 2012). I will argue later that the study may have been improved by extracting only the large scales variations from the data and perturbing randomly the mesoscales. 

The resulting maps of interpolated values, the only energy source of the simulation are not shown, which casts the shadow of a doubt on the realism of all the results obtained throughout the paper. Are we looking at observed mesoscale features or quasi-random (sampling-dependent) perturbations of a homogeneous density field? 

The validation against independent observations is unconvincing because these measurements are taken in the vicinity of the ice camp and are not representative of the remote unobserved areas. The authors correctly recognise that the validation is poor at the cross-over points but still boast uncritically the success of the validation in several places. This is not a major problem since the model is used for process studies which do not require any accuracy but the text gives a misleading impression of accuracy. 

The authors do not use any numerical model reanalysis nor climatology as background values, which is probably for the best to avoid additional artefacts. 

There are other aspects of the experimental setup that are should be clearly explained upfront in the paper rather than admitted too late in the discussion section. One is that the ocean is completely shielded from the atmosphere by an idealised ice cover, so that the only source of momentum in the model is the nudging to temperature and salinity. Another one is the breach of the continuity equation by the nudging, which contradicts the assertion that the assimilation is physically consistent. 

The data assimilation method itself is admittedly very rudimentary (nudging), but contains unexpected complications that are not justified at all: using different relaxation times for temperature and salinity and the odd-looking vertical relaxation coefficient in Eq (4). If these complications were necessary then the authors should explain what led to them. 

The paper writing is overall quite poor, even though the English is good, the explanations and justifications are often vague and the logic is not obvious. This is particularly true of the introduction, which reads as a long enumeration of unconnected facts. So the paper needs a thorough revision of the text to remove all the loose ends and strengthen the logic. 

Before the paper is acceptable for publication, the authors should provide visual evidence that the interpolated fields obtained by the inverse distance method are making sense as a quasi-steady-state estimate of the water masses or if any random perturbation of the homogeneous initial fields would have led to the same conclusions. 

The introduction should be completely re-written to prepare the reader for the experiments at hand and formulate more precise goals than to "extend current knowledge of submesoscale dynamics". The conclusions are just as vague: they are mostly reflecting a posteriori on the limitations of the experiments rather than highlight the newly gained insights related to the vertical EKE profiles. 

The paper has important scientific merits in spite of the abundant flow of criticism coming below, so I believe that it should appear after major revisions: new experiments would be an improvement but are not compulsory. However there should be a restructuring of the text, better explanations and a new figure showing horizontal interpolated Temperature and Salinity fields. 

Detailed comments: 

The abstract does not work as an abstract because it lacks most of the basic elements of context (What? Where? When? How?). 

On the contrary the five first lines do not belong in an abstract, but more in the introduction, and can be safely removed. 

- L8: The model is a major element of the study. The reader needs to know what kind of model is used: its nature (ocean general circulation without active sea ice), its name, the mesoscale-resolving resolution. 

- The time period of the study is missing, at least the season would be useful to know. 

- L12: Indications like East and West make no sense unless you mention the name of the area: the Nansen Basin, Amundsen Basin? 

- L12: "high variability" is also blue sky to the reader. High with respect to what? 

- L16 "the fields can be used for further analysis". That statement is very vague and should be made more specific once we have an impression of the degree of realism of the interpolated data. 

The introduction is an accumulation of facts taken from the literature. Although all of them are interesting in their own right, they cover a too broad scope to frame sufficiently the scientific context of the present study. They also read like an itemised notes from a literature review with no indication whether the findings will be revised by this study or not, and most of them are not. The logical succession of these facts is also left to the imagination of the reader. 

- L.50: Typically "An analysis of the dynamics of baroclinic vortices [...] is given in Sokolovskiy and Verron (2013)" does not tell whether this analysis is in any way related to the present paper. If the discussion does not loop back to it, then please remove it from the introduction. 

- L. 68: "Very high horizontal resolution" is too vague. Are they eddy-resolving, permitting, or event in the non-hydrostatic assumption? 

- L. 85: there are more than one interpolation technique. Since this part is criticising interpolation techniques, it is the adequate place to mention the one that will be used in this paper. 

- L89 to 97 the whole paragraph is a very cumbersome justification for using rudimentary rather than advanced data assimilation. If we trust your argument as it stands, there is no advantage to advanced data assimilation methods at all (nudging is more practical and yields better results) and nobody should ever be using anything else than nudging. Obviously you do not need to upset the whole data assimilation community to justify your choice of method. It is sufficient to state that 1) the costs and the complexity are not affordable in your case, plus 2) that the data coverage by a single quasi-random track is very unusual, so you lack evidence that advanced data assimilation is cost-effective in your case. Please rewrite the paragraph to better justify the choice of nudging. 

- L98: The goal of the study "extend current knowledge of submesoscale dynamics" is too vague. It is impossible to verify whether this goal has been attained or not. Please make it more precise. 

- L115: Indicate already here the vertical coordinate of the model is sigma rather than in Section 2.3. 

- L125: There is no thermodynamical effect of sea ice on the ocean, the next section will indicate that the ice drift is a constant value. A missing piece of information here is the sea ice area coverage, which seems to be 100% thus sheltering completely the ocean from the atmosphere. It should be made clear that there is no direct effect of the atmosphere on the ocean and that, after mentioning the constant lateral boundary conditions, there is no input of momentum to the model apart from the nudging term. As recognised somewhere far down in the manuscript. 

- L139: Is the value of 0.7 m/s set for the whole period and the whole model domain? Please explain why you have not made it more realistic. 

- L141: Why do you choose this definition of the mixed layer depth and why a minimum of 20 meters? 

- L159: Please indicate here the nature of the model boundary conditions. Not later. 

- L165: A boarder situation map with some topographic features would help understanding where we are. And where are the North and the East. 

- Figure 1a) is too small to discern all the details. I cannot see the cyan rectangle, maybe because I am colour-blind, but I suspect there is too much information on this sub-plot. 

- Figure 1b) shows a wide spread of T/S profiles, but only one density profile, which leaves us to imagine what the spread entails in terms of density changes. Can you include the spread of density still keeping the clarity of the plot. 

- L190: The duration of the experiment, 4 months, should have been mentioned earlier in the abstract and the introduction. 

- L195: The "ambivalence" is only a redundancy from the point of view of interpolation, but you could have exploited these crossing points as temporal information to calculate the errors related to the "quasi-stationary" assumption. 

- L198: the "quasi-steady-state" assumption is only mentioned in the "Nudging" section, when you cannot avoid it any longer, although it has been implicitly a major assumption since the beginning of the paper. Please formulate it upfront in the introduction and reflect on its implications for the study. 

- L200: high drift speed compared to the water velocity. The drift speed has been set to 0.7 m/s above, the velocities of 1cm/s are only mentioned in the discussion section. 

- L206: I can understand that submesoscale features of size 10 km located hundreds of kilometres apart are independent, but the mixed layer depths may change a lot within 4 months, please kill the suspense and indicate that this will be discussed later. 

- L210: The nudging term acts on temperature and salinity but the model currents are only corrected progressively through geostrophic adjustment, which makes the model inconsistent during the adjustment time (this is - by the way - an aspect better handled by advanced data assimilation than nudging), what is the typical timescale of this adjustment in your case? 

- L215: Why use two different relaxation time scales for temperature and salinity? What does that mean for the dynamical adjustment of the model to density changes? Can you at least indicate the values of the two time scales (Trelax comes later, but I cannot locate Srelax in the text)

- L221: Moving at 0.7 m/s, 2 minutes correspond to 80 meters (is this what you meant with "horizontal resolution"?) and are often within the same model mesh cell. 

- L228: The mathematics of spatial interpolation have progressed significantly since 1968. Maybe the inverse distance method combined with the kd-tree does perform well, but the choice is not justified here. 

- L230: The sharp transition between the cells that do and do not participate in the nudging should be mentioned here rather than in the end of the article. 

- Eq (4) looks like an inverse square distance interpolation in the vertical dimension but goes to zero in the separations between observed levels at depths. This seems excessively complex in the circumstances. Not relaxing between two observed levels seems prone to inconsistencies (unstable density profiles between two observed levels), a more intuitive solution would have been to perform vertical interpolation of the SIT profiles to the model levels (linear or cubic splines), ensuring the density increases with depths, and then relax with a single coefficient. The adequacy of the vertical interpolation should be better justified. 

- Eq(4) Is the surface temperature relaxed to the freezing point temperature or is that already handled by the FESOM model? 

- L238: Note here that a relaxation time of one day is considered very strong relaxation in practice. 

- L240: I imagine that the maximum distance changes together with the maximum number of values but please specify explicitly. Also mention the size of the largest and smallest neighbourhood tested. 

- L244: The deeper profiles are nudged over shorter distances than the shallow SIT profiles, making their effect probably negligible. This is counter-intuitive since the length scales are longer at depths. Please explain. 

- L247: No reason is given why the OC/PS profiles vertical relaxation is also different from the SIT profiles. Is it because these profiles have higher vertical resolution than the model? 

- L247: The model is nudged towards invariant temperature and salinity fields interpolated from the SIT profiles. These interpolated maps being the only external forcing of the model, they should be shown at a representative depth, for example the salinity above the halocline (20m or 50m) and the temperature at 100 m. 

- L249-250: These technical details can be removed. 

- L256: The "small time resolution" of the instruments should probably be called "low frequency sampling".  

- L260: The PS-CTD profile in Figure 1 is not a typical profile as it is both warmer and more saline than all the other profiles, so it is not obvious if this profile is overall more stratified or more unstable than the profiles that will be assimilated later. If you plot all density profiles as thin lines, you can give an indication if the assimilation will have a stabilising or destabilising effect overall. 

- L265: It is very well that the authors admit the breach of the continuity principle, but this should have been admitted earlier in the methods description. More advanced multivariate data assimilation methods may mitigate that problem, which could be worth noting in the discussions. Alternatively, the authors could have calculated geostrophic current velocity increments from the density gradients caused by the nudging term, by analogy with the Cooper and Haines (1996) method. 

- Figure 4 sections show discontinuities in the vertical salinity profiles, are these real or are there only a few bands in the (very small) colour scale? 

- L286: This sentence is a very contorted way to acknowledge the temporal evolution of the ocean variables. Again, it is regrettable that the cross-over differences have not been exploited as mentioned earlier. 

- L297: "Same order variability at the model grid scale" this variability is not visible in Figure 6, has it been smoothed? 

- Section 3.2 T/S reconstruction contains lengthy descriptions. Please reconsider if they can be shortened. 

- L300-301: Unclear sentence about the slope being "deeper than 40 m". Please rephrase. 

- L304: Why is the bulge associated with mesoscale features? 

- L306: "characterise the simulated system as isotropic". Unclear as well, please rephrase. 

- L315: Only here do the authors first admit that the EKE collapses by construction of the model. Knowing that the nudged EKE is resulting from an interpolated dataset containing both temporal and spatial variations and not strictly "steady state", I would expect that the resulting EKE would initially be too high. Remember that the interpolated fields are not shown so the readers are free to imagine what has come in there. So please show the interpolated fields and indicate - even roughly - the a priori expected range of values of EKE that should be reasonable. 

- Figure 7a) shows tiny mesoscale features but a lot of the areas are white. It should be rotated (the X and Y axes have not meaning anyway) and cropped to maximise the useful area. 

- Figure 7b) I cannot see the yellow solid lines. Try making them thicker. 

- Figure 8 also has too much white area. Rotate and crop for clarity. 

- Figure 9 is very nice and even shows internal waves that are not discussed in the text. This could be added if space permits. 

- L345-349: Is the description of the eddies movements necessary for the rest of the paper? 

- L359-361: This argument does reach any conclusion, so I will give you mine. The ice drift change direction in the Northern part but the model forcing was constant, however the data coverage is more complete where the ice drift is sinuous. This means that the data sampling affects the simulated vortices, which should be more abundant to the top part of the graphs. 

- Section 4.3 "Method limitation" does not discuss much the limitations arising from the results but mostly limitations by construction that could have been flagged upfront in the method description instead of leaving the readers wonder about them throughout the paper. Paragraph 369-378 is probably the only proper discussion of the results and should stay there. 

- L374: What do you mean by "displaced"? 

- L379-385: According to the previous paragraph, the large-scale gradients can be trusted as "instantaneous" (or synoptic), but not so much the small scales. So a solution following Robinson et al. 1996 could be beneficial here: the large-scale component of the interpolated data can be used for nudging, while discard the small-scales, which can be excited by random mesoscale perturbations all over the model domain, thereby removing the "internal boundary". 

- Same paragraph: The same remark applies to the vertical interpolation since you have used a similar square distance function with only 3 meter characteristic depths. An "internal boundary" in the vertical may a priori have more adverse effects on this study. 

- L384-395: I thought that you already did a sensitivity analysis to the influence radius, did you not test a larger radius? 

- L388: It is clear that 1cm/s is much smaller than the 0.7 m/s ice drift but that could be noted upfront. The general direction of the currents could be indicated as well for information. 

- L410 The number 630.000 may seem quite impressive but still does not make a proper synoptic measurement campaign. Please acknowledge that. 

- L412 As noted earlier, the measurements are not independent if they are located within one Rossby radius of the assimilated profiles. There are spatial autocorrelations that reduce the significance of the validation. 

- L417: I would not claim that these are "dynamically consistent" as long as the measurements are collected along a 4-months trajectory across moving eddies. You have criticised the "quasi-stationary" assumption earlier so you should moderate this claim accordingly. 

- L421-422: Here would be the adequate place to recap these insights. I can note the vertical maxima of EKE in the Atlantic layer and the halocline. These findings may have been noted by earlier studies but it is still good to confirm or contradict earlier papers. 

- Code and data availability: Are the in situ profiles publicly available?

Typos:

- l28: add a comma between Basin and Zhao. 

- L. 80: DN is undefined at this point. 

- l82: close the parenthesis after Fang et al. 2023 (submitted). 

- L.121: Li et al. misses a year. 

- L138: Define ML as Mixed Layer. 

- Eq (1) indicate that z is the depth, positive downwards. 

- Figure 4: The subplots labels a, b, and c are wrong in the caption. They should be b, c, and d. 

- L303 "low-salinity (high-density) intrusions": should this rather be "low-density"? 

- L340 "and about 5 km" is missing an "is". 

- L425: "The rest". 

- The reference to Sokolovskiy and Vernon has duplicate title but no journal name nor volume number. 

References :

Bourgain, P., & Gascard, J. (2011). The Arctic Ocean halocline and its interannual variability from 1997 to 2008. Deep Sea Research Part I: Oceanographic Research Papers, 58(7), 745–756. https://doi.org/10.1016/j.dsr.2011.05.001

Cooper, M., & Haines, K. (1996). Altimetric assimilation with water property conservation. J. Geophys. Res, 101, 1059–1077.

Robinson, A. R., H. G. Arango, A. J. Miller, A. Warn-Varnas, P.-M. Poulain, and W. G. Leslie (1996), Real-time operational forecasting on ship-board of the Iceland-Faeroe Frontal variability, Bull. Am. Meterol. Soc.,77, 243–259. 

Troupin, C, Barth, A, Sirjacobs, D, Ouberdous, M, Brankart, J.-M, Brasseur, P, Rixen, M, Alvera Azcarate, A, Belounis, M, Capet, A, Lenartz, F, Toussaint, M.-E, & Beckers, J.-M. (2012). Generation of analysis and consistent error fields using the Data Interpolating Variational Analysis (Diva). Ocean Modelling, 52-53, pp. 90-101.

Zimmerman, D., Pavlik, C., Ruggles, A. et al. An Experimental Comparison of Ordinary and Universal Kriging and Inverse Distance Weighting. Mathematical Geology 31, 375–390 (1999). https://doi.org/10.1023/A:1007586507433