General comments

This manuscript is a valuable contribution to the literature. The authors bridge small-scale ocean modeling studies with larger-scale ocean modeling by proposing a new variant on a parameterization of ice-shelf melting. They then assess this parameterization against local observations of ice-shelf melting and remote-sensing-based estimates of ice shelf melting at one ice shelf. They also demonstrate the parameterization’s impact on ice-shelf cavity dynamics through cavity-scale ocean modeling in an idealized domain previously used in the literature. I believe that this parameterization has the potential for becoming the state-of-the-art. However, I do think at times the key points get lost in the text, and I offered some suggestions for improving the communication of the author’s results. The main scientific deficiencies I see are an insufficient comparison of Pine Island Glacier simulated melt rates compared with remote-sensing products and a lack of clarity on whether the state of scientific knowledge supports the adoption of your MK18 low-velocity limit variant of your parameterization. As a result, I think these qualify as major revisions but I would emphasize that the quality of the science in this manuscript seems to be high.

Specific comments

Consider moving Section 2.4 to early on in the Results. 

Consider moving either of the MOM6 or MITgcm idealized simulations to a supplement/appendix. Given that they are qualitatively similar, it may be best to try to de-clutter the main text a bit.

L150: It's worth highlighting sooner that the evidence suggests a greater response to stratification than any of the current parameterizations feature.

L152: It’s not clear why you are discussing the uncertain drag coefficient. I think it’s helpful to give readers a sense of where you are going with all of this. E.g., that you will be proposing a different parameterization for \Gamma_T and \Gamma_S and leaving c_d as a tunable parameter.

Since you choose L=2500 as the cutoff for the shear regime, it’s not clear why you are computing the best fit line without a floor at this value

L205: Check that equations yield the constant coefficients when L<0 (i.e., that the first term isn’t negative)

L554: “However, stratification feedback effects were seen” Elaborate on this point.

L714: “the local slope angle can be calculated from the ice base taking the maximal local angle” If I interpret this appendix as a guide for implementing MK18 in models, then I would want to know whether this approach is going to be sensitive to the effective horizontal resolution.

I didn’t love how the axes of Figure 3b didn’t match those in Figure 2. It made it difficult to tell where in the T-u* space we have obs constraints. Consider changing axes or plotting the obs points on one of the figure 2 panels.

In section 4.4, you first present results without tuning C_d, which do not match observed melt rates, and then tune C_d to match observed melt rates. The untuned results are less relevant to how the community would go about regional ice shelf cavity modeling. Thus, I would argue that you should only present the results from the tuned simulations in the main text and move a comparison of the parameterizations with the same drag rate to a supplement or appendix. 

One of the main arguments in favor of adopting your proposed parameterization is that it produced a more realistic distribution of melt rates at PIG. Thus, I think it’s really important to plot the results from one of the observational products you cite in the paper compared with your simulated melt rates with and without StratFeedback. (The motivation for this parameterization is also a bit weakened by your statement that Nakayama does a good job at representing melt rates.) RMS would be a relevant metric to compare these simulations, and a figure with a PDF/histogram of melt rates could be instructive if there are significant differences for the same mean melt rate.

I think the reader could benefit from a little more discussion of the IOBL in the MITgcm PIG simulation, such as what properties look like over the layers that are sampled for the parameterization for the base case vs. the StratFeedback case. The friction velocity shown in Fig. 10e provides a partial understanding. 

It’s quite unclear what readers are supposed to take away from your low-velocity limit experiments. You say “​​We have proposed one option for a transition to a velocity-independent convective parameterisation at low velocities” but this statement is so neutral. It would be more helpful to readers if you explained the pros and cons of this option in the discussion so readers can make an informed choice for themselves. But on the other hand, there appears to be so little that can be used reliably to evaluate the MK18 parameterization that I was left wondering whether it was worth devoting so much space in the paper to it. You seem to be arguing that the ISOMIP+ experiment is not a good one for evaluating the MK18 parameterization. You mention that the PIG MK18 simulation increases melt rates, but it’s unclear whether adding MK18 yields an improved melt rate distribution relative to observations. Furthermore, it wasn’t clear whether any of the observational estimates shown in Figure 3 could be used to assess MK18. (If so, consider discussing and plotting these symbols as well for those affected.)

A point that you make but gets a little lost in the text is that the parameterization is not optimal for DDC regime but yet it likely improves the accuracy of predicted melt rates in that regime by reducing melt rates. If I am understanding this correctly, I would encourage you to emphasize this.

Technical comments

L9-10: “which accounts for stratification suppressing the turbulence that drives basal melting” clunky

L53: or >> nor

L58: “Other simulations…” sentence too long

L68: “However, inaccuracies” too many different ideas in this sentence

L85: Insert “Kerr and McConnochie (2015) parameterization which captures”

L91: Somewhere around here, make it clear that you are focusing on Antarctic ice shelf conditions

Table 2: I think it would be helpful to pull this out into a numbered equation so that it is more clear to readers how to transition between the two regimes.

L224: Somewhat confusing to call it a different parameter choice in some places and a different parameterization in others

L230: H99 >> H99-M81?

Fig 2a: There appears to be a difference across parameterizations in the high u*, high T* regime but the legend is hiding those contours. Move legend for panels a and b, ideally.

L234: use LES abbreviation sooner or keep unabbreviated name here

L346: “bulk mixed layer” as defined by?

L458: “gives us confidence in our simulated melt rates” This is an odd way of putting it. I assume you mean confidence that you have implemented the parameterization as intended?

L476: “(indicated by… ” Move parenthetical next to the figure reference

L501: “This reduction…” should figure 10f be cited here?

Fig A1b Is it difficult to get useful information from HJ99-M81/CC? It is a little weird that all the other panels but this one are ratios with respect to CC.

Fig A1d: I think it would be helpful to have a contour somewhere near the minimum value in panel (d). The light blue values can be hard to make out.

The authors use data from published LES experiments to develop a parameterization to diagnose vertical fluxes of heat and salt through the oceanic boundary layer at an ice shelf base. The improvement they make is to account for the way stratification can cause suppression of the vertical transports, generally in warm and relatively quiescent environments; however, they make the case that some ice shelf cavities with only weak thermal driving are also likely to be affected by stratification in the same way, and simulations of such cavities would also benefit from using the improved parameterization.

They apply the parameterization to two ocean models, run within the MISOMIP+ framework, comparing with other routinely used parameterizations. They also apply one of the models to the cavity beneath Pine Island Glacier, again with their own and one other parameterization.

I am not a modeller, but I find the paper well-written, generally easy to follow, and the results are convincing. It’s a relatively simple story, but has some important implications, one of which concerns the utility of the MISOMIP+ setup that they adopted. I would like to see it published, with some minor revisions.

I’m submitting a marked-up pdf. There are several minor suggestions that might help improve the clarity of the text, but the authors should feel free to ignore any or all of them. 

There are a small number of more substantive comments in the pdf, which I will repeat here, along with some other general remarks. They mostly don’t require revisions, perhaps a little more explanatory text.

The authors extend their parameterization for very low velocities using a formulation based on laboratory and DNS experiments. The authors who developed the lab-based parameterization note that it is not recommended for basal slopes of less than 10 degrees, a caveat also pointed out by the present authors. As the basal slopes that can be resolved by the vast majority of models are at least an order of magnitude smaller, this is clearly an inappropriate extension. I see that the authors want to extend the parameterization somehow, but using one developed for a different regime might not be wise: the fact that it came from a study gives its application the cloak of respectability when it is simply inapplicable. I would prefer to see an arbitrary set of transfer velocities used at low velocities, possibly tuned in some way. I’m sure the authors wouldn’t want to make such a change, but I would be interested to hear their response.

A more general remark about the way the different regimes are discussed, particularly the “velocity-independent” regime described by MK18. My understanding of the way this is discussed is that we can have some sort of regional external forcing (eg a coastal current flowing beneath a small ice shelf); tidal forcing (also largely externally-forced); and then a buoyancy-driven current, where the forcing comes from melting within the cavity. When that melting is occurring locally, that latter case is what seems to be called “velocity-independent”. Which means that it’s independent of the free stream velocity, the velocity outside the boundary layer. In old parlance, it’s what was called a gravity plume. If my understanding is correct, I think the terminology is confusing and I encourage the authors to make the point that the parameterisation is not so much velocity-independent, but rather, it’s free-stream velocity independent. If I’m wrong, then please educate me. Am I the only one confused by this? Possibly.

Mainly in section 2, the authors use a variety of different terms to describe distance from the ice base, particularly with respect to velocity. We had “far field velocity”, the velocity in the “uppermost part of the boundary layer”, the “upper layer velocity” and the “mixed layer velocity”.  Although I got the general sense, it would be nice to attempt to standardise, or perhaps define these terms more precisely. Similarly, when describing the way the two models handle the upper part of the water column, a bit more clarity about how the levels for water speed and temperature are selected would help.

In the Pine Island Glacier cavity modelling the authors chose to tune Cd to give a good comparison with HJ99-neutral. Why did they not choose one of the satellite-derived melt rates? I guess it depends on the purpose of the experiment, but again, it seems like a free choice, and a result closer to what we think of as reality might have been more useful. Just a question. A sentence in the text to explain the choice would be good.

(A bit of a detail. In the fit to derive the StratFeedback parameterisation (from Figure 1) why do the authors adopt natural logarithms in the formula? No problem, but it seems to be a free choice, and they are plotted using logs to base 10.)