Review of “A numerical investigation on the energetics of a current along an ice-covered continental slope” by Leng et al.

In this manuscript the authors build on recent work exploring the impact of sea ice cover on ocean dynamics and baroclinic instability. The simulations are well chosen, the theoretical work is generally clear, and the results are compelling.

However, I think the manuscript would be easier to read if it were slightly restructured.  I also have a few minor suggestions.

Edward Doddridge

Comments

Structure and story

The manuscript contains a lot of great science, however, it is not as easy to read as it could be. The names of the control and sensitivity experiments are all very similar, and the current structure requires readers to remember all of the different simulations and use that knowledge while reading all of the paper. The paper would be easier to digest if the sensitivity experiments were introduced in section 3.2 when they are discussed.

Eddy spin down

There is a wealth of previous work examining the impact of surface stress on mesoscale eddies outside of the sea ice zone. The manuscript would be strengthened by engaging with this literature, for example Munday et al. (2021) and Seo et al. (2019), and the references within. In particular, the discussion in lines 366-367 would benefit from this addition.

Minor comments

Line 85: The description of the initial velocity state would be clearer if equations 1a) and 1b) were swapped. As written, the x dependence of the initial velocity field is not immediately obvious – I spent longer than I care to admit looking for an x in the right hand side of 1a).

Lines 104-105: positive downward radiation would act to melt the ice, not maintain it.

Line 136: This should be rho_0 to be consistent with the Boussinesq approximation used by MITgcm. E.g Nycander (2011).

Line 149: why is the power from the ice friction an estimate? These variables can be directly obtained from the model and power calculated exactly.

Line 161-162: A statement regarding the magnitude of the relative vorticity would help justify ignoring the relative vorticity of the mean flow.

Lines 239-243: This paragraph is poorly phrased. The phrase ‘steady state’ is used to refer to the evolving state prior to the generation of eddies – this is not a steady state since the flow and density surfaces are evolving. Only in an actual steady state would the intersection of streamlines and density surfaces require a diapycnal transport.

Line 281: “maintains”? Should probably be ‘remains’ or ‘is’.

Lines 288-289: Does interior friction refer to viscosity?

Figure 11e): It may be a plotting issue, but it looks as though the work done by the surface stress is larger than the reduction in mechanical energy at the start of this panel.

From day 100 onwards, it looks as though the ice-ocean stress is putting a small amount of energy back into the ocean. What is going on here? Has the mean current reversed?

Lines 355-360: The figures for mechanical energy are very instructive. Can similar time series be constructed for the APE? This would explicitly show the changing importance of Ekman pumping and baroclinic instability.

Lines 366-367: Discussion of previous work on eddy spin down would be appropriate here

References

Munday, D. R., Zhai, X., Harle, J., Coward, A. C., & Nurser, A. J. G. (2021). Relative vs. Absolute wind stress in a circumpolar model of the Southern Ocean. Ocean Modelling, 168, 101891. https://doi.org/10.1016/j.ocemod.2021.101891

Nycander, J. (2011). Energy Conversion, Mixing Energy, and Neutral Surfaces with a Nonlinear Equation of State. Journal of Physical Oceanography, 41(1), 28–41. https://doi.org/10.1175/2010JPO4250.1

Seo, H., Subramanian, A. C., Song, H., & Chowdary, J. S. (2019). Coupled effects of ocean current on wind stress in the Bay of Bengal: Eddy energetics and upper ocean stratification. Deep Sea Research Part II: Topical Studies in Oceanography, 168, 104617. https://doi.org/10.1016/j.dsr2.2019.07.005

The manuscript by Leng, He and Spall looks into what releases Available Potential Energy (APE) in the Chukchi Slope Current. They build on an earlier paper by Leng, Spall and Bai (LSB) which pointed to how ice-ocean friction impacted the current. In this new manuscript the authors primarily compare the importance of mean friction-induced overturning to eddy overturning (by baroclinic instability) in reducing APE. They use idealized numerical model simulations to study the fully nonlinear adjustment in a set of spin-down experiments. They then conduct linear 1D quasi-geostrophic (QG) stability calculations to assess the baroclinic instability properties of the flow. The conclusions are that the large-scale frictionally-driven overturning is at least as large as the eddy-driven overturning in releasing APE.

I find that the study will make a useful contribution to our understanding of Arctic Ocean dynamics and, particularly, of how mesoscale eddies and sea ice impact the circulation. The study is for the most part well conducted and well written, so I will recommend that the paper is eventually published. There are nonetheless several issues that I would like the authors to address, both scientific and stylistic. I consider none of these to be crucial. But there are quite a few of them, and for this reason I will suggest that a 'major revision' is needed.

In the following I will address the authors directly:

1 (l 67): It is claimed that the resolves mesoscale eddies. Here I expect you to define what you mean by 'mesoscale'. And if you mean that the first internal deformation radius is resolved well, then you'll need to report on how large this is, ideally both in the real Arctic and in your model.

2: Is these pure spin-down experiments? Please clarify.

3 (l 103): How is a downward radiative flux maintaining a sea ice cover? And does this buoyancy forcing imply that the model is in fact forced (so not pure spin-down experiments)? I also note that the surface mixed layer depth is kept to a minimum. How does this then contribute to the overall forcing of the model?

4 (l 143 + eqn. 6): Here (in the definitions of KE) only v (north-south) is used. Is this because the expressions pertain to the mean flow? The north-south-averaged u should be small but not necessarily zero at every instance in time. Please clarify/discuss.

5 (l162): Background relative vorticity is ignored in the 1D QG calculations, as it needs to be. But I would like to see some rough scaling showing that this is a safe assumption. The reader might wonder since the relative vorticity of the mean flow is central to the other aspect of the dynamics studied here, namely the uneven surface Ekman pumping.

6: In the stability calculation, only north-south wave propagation is accounted for (k=0). Admittedly, these are likely the fastest-growing waves. But please discuss this briefly.

7: The instability machinery assumes QG. It then makes no sense to study wavelengths down to 1 meters, as done here. A point should be made of this, i.e. that one cannot assume QG to be valid down to this range.

8: You might try to study growth in log scales in Fig. 5 to investigate whether you observe an exponential growth stage at any time. This might help a bit with the discussion on the bottom of pg. 5 and top of pg. 6. Just a suggestion.

9: In Fig. 6b, would the fit between EKE and the eigenvector improve at all if you plotted the square of the eigenvector (as energy is a squared quantity)? In other words, to get at EKE profile from the linear modes, you would have to square.

10 (l 229-32): The explanation for the emergence of the subsurface depth could be clarified. How would this overturning remove the surface maximum?

11 (l 240-42): There is no steady-state ever in these simulations, right? But really my problem is with the sentence "...the surface velocity and overturning are very weak and there are no vertical...". Please check and clarify.

12 (l 253-54): Here it is argued that the halocline mode extends to the surface. But earlier you claim that this mode is sheltered from the ice friction. How do these statements relate?

13 (l 256-57): In Exp-PD100 the subsurface KE maximum at ~100m depth is also clearly reduced immediately after introducing friction at day 100 - even if less so than higher up. So you may want to modify/qualify your sentence discussing this experiment here.

14 (l260-61): How is the large-scale Ekman pumping (releasing APE) a source of EKE? Clarify.

15: In your discussion of Fig. 8 you focus first on KE (top panel) and then on APE (lower panel). The time-evolution of both quantities are of course intimately related. I, as a reader, would prefer that you discuss the time evolution of KE and APE simultaneously - as you go through experiment by experiment. An extra note: for the APE discussion there are at least a couple of experiments (PD & PD100) that you don't discuss. Make sure you mention at least something about all lines in these plots.

16 (l265-67): The APE in Exp-P continues to decrease also after day 100, i.e. after the KE field has plateaued. Discuss.

17 (l 269): How about defining total mechanical energy (you use it later as well) as "the sum of APE and KE"?

18 (l 270): What is 2-dimensional about the flow without eddies?

19 (l 271-72): The APE of Exp-PF is *slightly lower* than in Exp-PD after eddies form. This is likely for the same reason as for why KE in this experiment is higher, namely that eddies are not damped. Eddies also contribute to APE release and are, presumably, more efficient at this in Exp-PF.

20: Is Fig. 10 mentioned in the text at all? This is a big figure and deserves a few lines of mention.

21 (Eq. 11): I would rather say "...which assumes that...". But, more importantly, you will need to convince me that Eq. 11 is a QG form of the density equation. The QG formulation normally includes horizontal advection by the geostrophic flow. As I understand things, it's only when the lateral flow is ageostrophic (e.g. after integrating zonally around a periodic channel) that it may scale to be small compared to vertical advection of the background vertical density gradient (as e.g. done in Vallis's book on pg. 387).

22 (l 303...but also other places): You write that g(rho-rho_r)*w is the vertical buoyancy flux. But there is at least a sign inconsistency here and even (to be pedantic) a unit problem. Buoyancy is defined as b=-g(rho/rho_0). So I suggest you define a proper buoyancy flux or you remove the 'g' and call it a density flux (also later in the text).

23 (l 302-03): There is awkward wording here: upwelling...upward and downwelling...downward. Please rewrite.

24 (l 305, 312 and Fig. 12 caption): Related to my comment 22 above. A buoyancy flux which will release APE is positive, not negative. The density flux is downward.

25 (l 313-14): "...so there is no need for the loss in mechanical energy." I would disagree with such an interpretation. It's correct that b.c. instability produces EKE from APE (actually, in the Lorentz energy cycle the transfer goes via EAPE). But of course total mechanical energy is lost eventually there too, via friction (ice, bottom, internal). And, actually, even your large-scale flow probably needs to go through such a route. How can the APE which is released by the large-scale Ekman pumping eventually be dissipated? The only route to dissipation goes through KE. So I urge you to think through whether you need to rephrase some of these statements.

26 (l 321-27): This discussion of frictionally-induced Ekman pumping tied to existing eddies is not very convincing. To say something convincing here, especially about the net impact on vertical buoyancy flux, I'd say you'll need to average over lots of eddy motion. You've already defined eddies in a Reynolds sense as the deviation from the along-channel (north-south) mean. Could you do a Reynolds flux calculation, with and without friction applied to the eddy field?

27 (Fig. 14a): Are the background isopycnals (dashed lines) actually as flat as they appear here? I don't see anything which would suggest a thermal wind shear here.

28 (l 346): Should the expression for R_BC have a H^2/L^2 in it (instead of H/L^2)?

29 (l 357-59): Note that here you mention a scale transition of about 10 km. But in both the abstract and the Summary section you talk of the (internal) deformation radius. If you want to mention the deformation radius anywhere in the text, you'll need to build up the story around it somewhat. Is 10 km approx. equal to the def. radius in your simulations. And why would this scale be the important scale? Note, by the way, that halocline eddies need not take the scale of the def. radius since they do not extend throughout the entire water column. The instability producing halocline eddies is not pure Eady instability involving top and bottom edge waves. So it's not obvious that the classical def. radius is a relevant scaling parameter for the problem.