|Review: `Tidal Modulation of Antarctic Ice Shelf Melting, Revision 1’ by Richter et al.|
The authors have substantially revised this manuscript in response to the original round of reviews, and overall it has substantially improved. Below I have listed several further comments and questions, largely aimed at clarifying aspects of the manuscript and the caveats to the authors’ modeling approach. My most major comment concerns the authors’ decomposition of the ice shelf melt rate into dynamical and thermodynamical drivers. Specifically, I am concerned that the authors’ decomposition may be strongly sensitive to the order in which the difference is taken between simulations (quantifying the effect of adding tides vs. the effect of removing tides), and thus may be producing a misleading partitioning of the dynamical and thermodynamical contributions. Below I explain this concern in detail and suggest an approach that circumvents this issue. This issue has the potential to require wide-ranging changes to the manuscript’s figures, text and conclusions. While I consider this an important issue, I am confident that the authors can resolve it after another round of revisions.
L6-7: I had to read this sentence several times to parse it properly. I suggest rephrasing.
L86-88: The prescribed surface fluxes are “accurate” in the sense that they are consistent with observations, but I am not convinced that this is an “advantage”, as the fluxes may be inconsistent with the simulated state of the ocean. For example, negative heat tendencies may be applied to waters that are already at the surface freezing temperature, producing super-cooled waters (presumably the authors have implemented a fix for this issue). Or surface currents could be accelerated by the imposed momentum fluxes in regions where the sea ice is thick and largely immobile, and should be retarding the near-surface flow. I do see the advantage in ensuring that the area-integrated buoyancy gain and loss is correct in different parts of the continental shelf, but I find it misleading to describe this as “accurate”. The authors should rephrase the text to be more candid about the advantages and disadvantages of this approach.
L87-94: Have the authors compared the buoyancy fluxes that result from these modifications with the buoyancy fluxes derived from Tamura et al. 2011? Do they substantially modify the surface fluxes in any particular regions?
L106: Please specify which month(s) the 30-day analysis period occurs in. The authors should also discuss potential sensitivities to performing this analysis in summer vs. winter months. If the analysis is performed over multiple 30-day periods to span the full simulation duration then this should be stated.
L145: I do not understand this sentence: please clarify.
Fig. 2: I suggest using fewer color graduations in the colorbar to make it easier to read values in these plots, particularly panel (b).
Fig. 4: I assume that the barotropic velocity here is defined as the magnitude of the depth-averaged velocity vector - is this correct? In panel (b), how is the continental shelf potential temperature defined - surface, bottom, or depth-average (or something else)?
L180-188: I am concerned that the authors’ formulation of the dynamical/thermodynamical decomposition may be producing misleading results here. The core issue is that their decomposition (eqn. (5)) may produce qualitatively different results depending on whether they subtract the no-tides (nt) case from the tides (t) case or vice versa. Consider these two approaches:
Approach 1, quantifying the change in heat flux due to adding tides:
w_b,t - w_b,nt ~
u_nt (Delta t) <thermodynamical>
+ (Delta u) T_nt <dynamical>
+ (Delta u) (Delta T) <covariational>
Approach 2, quantifying the change in heat flux due to removing tides:
w_b,nt - w_b,t ~
- u_t (Delta T) <thermodynamical>
- (Delta u) T_t <dynamical>
+ (Delta u) (Delta T) <covariational>
In each case Delta u = u_t - u_nt and Delta T = T_t - T_nt.
Clearly the covariational term is insensitive to the order of the subtraction. However, the thermodynamical and dynamical terms may be. For example, in order for the thermodynamical terms to be comparable, we require
u_nt (Delta_t) ~ u_t (Delta_t)
=> u_nt/u_t ~ 1
=> Delta t << u_nt, u_t
However, the addition of tides is likely to create situations in which u_nt is approximately zero, but u_t is on the order of 10 cm/s. In such situations, Approach 1 will yield a very weak thermodynamical contribution (perhaps explaining Fig. 5c), whereas Approach 2 will yield a large thermodynamical contribution.
For a concrete example, take
u_t = 0.11 m/s
u_nt = 0.01 m/s
T_t = 0.5 deg C above freezing
T_nt = 0.3 deg C above freezing
Delta u = 0.1 m/s
Delta T = 0.2 deg C
Approach 1 yields
Approach 2 yields
<thermodynamical>: - 0.022
<dynamical>: - 0.05
Total: - 0.052
With approach 1, we conclude that <thermodynamical> is an order of magnitude weaker than the other contributions. With approach 2, we conclude that <thermodynamical> is comparable to the other contributions.
It is not clear whether the authors have considered this, so I would ask that they revisit their decomposition in this in mind as they revise the manuscript. My suggestion would be that they decompose the heat flux by defining
u_m = (u_t + u_nt)/2 and T_m = (T_t + T_nt)/2,
w_b,t - w_b,nt ~ (u_m + Delta U/2)(T_m + Delta T/2) - (u_m - Delta U/2)(T_m - Delta T/2)
= u_m (Delta T) <thermodynamical>
+ (Delta u) T_m <dynamical>
This eliminates the covariational component and ensures that the thermodynamical and dynamical components are insensitive to the order of subtraction.
L209: “While circum-Antarctic total melt is small” - is it? Did the authors mean to refer to the change in melt due to tides instead?
L213: “strongest changes” - meaning changes due to the introduction of tides? This needs to be clarified because as currently written this is likely to be misinterpreted as changes with time.