This paper presents a model/data comparison looking at ice-shelf flexure at Priestley Glacier in Antarctica. The authors use a series of differential interferograms to estimate tidal displacement and examine the spatial pattern of these displacements. The time series is validated with GPS from 2018. They compare the observed displacements with three models of elastic flexure, which vary in terms of their assumptions about the geometry of the problem (ice thickness) and about the Young’s modulus. From this comparison, they argue that the shear margins are extremely weak (20% of the expected strength). They conclude that DInSAR can be used to understand shear-margin strength.

The paper is likely to be of interest to the readership of The Cryosphere. It is reasonably well written, though I need some clarification at a few points, and the figures are clear and support the narrative (though some small changes are needed for legibility). However, I am skeptical of the conclusions, as described in “major issues.” Specifically, I think the central claims in the abstract are not supported by the results, and it is unclear to me how the results will hold up to more careful checks on their robustness. I also have some reservations about the claims about the physical origins of this signal, assuming it is robust—I do not think fabric is the likely cause. If the authors can demonstrate that the signal of shear-margin weakening is not a byproduct of their assumptions but rather a robust feature of the data, and the fabric-related conclusions were either better supported or removed, I would be supportive of seeing this work in The Cryosphere.

Major issues

Unless I have missed something essential, the central claims of the paper as presented in the abstract are not supported by the results. The abstract claims “we find that

a five-fold reduction of the Young’s modulus in the shear zone, i.e. an effective shear-zone weakening, reduces the root-mean-square-error of predicted and observed vertical displacement by 84 %, from 0.182 m to 0.03 m.” However, it seems this number is derived by comparing the unmodulated tidal height to the observed displacement, which fails to account for any elasticity. From line 386, it is clear that the 0.182 is the unscaled tidal forcing. In fact, the local heterogeneous model underperforms the local homogeneous one (0.029 vs 0.027 m misfit), so it would be more appropriate in the abstract to say that shear-zone weakening is unable to improve the fit! The central claim of the paper instead needs to rest on the comparison between the local homogeneous (or perhaps control) model and the heterogeneous model—this is what tells us the effect of the shear-zone weakening. All that can really be said based on the misfit is that an elastic model is useful—nothing about the three different models is conclusive with regards to misfit, as acknowledged by the authors at line 333. The matching claim in the conclusions (“we demonstrated that reducing ice stiffness in lateral shear zones significantly improves the accuracy of vertical displacement predictions, particularly along the grounding zone,” line 477) is also unsupported by the results.

The problem with the misrepresentation above is that it forces the authors to wade into a more complicated comparison in terms of alpha. More physical explanation of alpha is warranted, as discussed in the general comments below, but in terms of the effect on results doing the comparison in terms of alpha obscures the effects of uncertainty and error. We need a careful analysis of these uncertainties and errors to understand if the comparison in terms of alpha is in fact meaningful—as is, I find the error analysis in the paper insufficient. I do not think a single, fixed value of E to treat as a reference that easily justified (for example, the 2019 paper by the same authors has 1.0±0.56 in the abstract). I do not see how the authors can exclude the possibility that there is substantial variation in E because of things like temperature, and that the mean value is incorrect, which in combination may explain much of the misfit. Similarly, the conclusions of the paper rest on the better fit of the model with weakened Young’s modulus in the shear margins, but there is not systematic evaluation of how changes in Young’s modulus affect the misfit. Maybe reducing the value elsewhere would produce a better fit—we simply do not know. Without a more systematic comparison, and without a clear evaluation of how uncertainty in the parameters assumed constant affect the results, I am not confident that we can in fact conclude that the authors robustly detect a signal in the shear margins.

I also do not buy the argument that fabric is likely to explain these observations. The authors conflate the viscous anisotropy of ice, which is very strong (an order of magnitude weakening or hardening) and anisotropy of the elastic properties, which are much weaker. There has been extensive work on this topic in the seismic literature, so we have a reasonable number of measurements of the effect of fabric on seismic wave speed, which have found values in the range of 5% and below (e.g., Lutz et al., 2022 https://doi.org/10.5194/tc-16-3313-2022, Rathmann et al., 2022, https://doi.org/10.1098/rspa.2022.0574, and many references therein). Since seismic waves are elastic, I would expect the effect of fabric on ice shelf flexure to be similar to its effect on seismic waves, i.e., about 5% rather than the 80% needed to explain the results here. As a starting point, I suggest looking at Rathmann et al., 2022, since they formulate the effects on elastic anisotropy in terms of the anisotropy in the Lamé parameters, which could relatively easily be converted to anisotropy in the Young’s modulus and Poisson ratio, and it appears that the value would be on the order of a few percent. Thus, I think section 5.2 should be reworked to acknowledge the limited effect of fabric on elasticity, and to propose alternatives. Most obvious to me are things like thickness errors, damage, and errors in the value of E used as a baseline. Alternatively, if the authors think this is really a viscous effect, then the validity of the purely elastic model is called into question. The conclusions should be changed to reflect this viscous/elastic difference. I am not convinced that there are grand implications for ice-stream initiation and would certainly need to see more discussion in section 5 if this were to remain in the conclusions.

General comments

The least-squares adjustment needs more explanation. It is a bit strange to do least squares with an underdetermined system—I guess this amounts to trying to adjust the tide model as little as possible? What this assumption implies deserves explanation. However, I am confused as to how the misfit is not reduced to zero when the system is underdetermined—is this system of equations not linearly independent? A sentence explaining why there is any residual misfit would help clarify.

I am a bit unclear how the load tide is handled. Is the bed underneath the grounded portion of the glacier truly assumed fixed, so that w=0 there? Or is the load tide assumed to apply only where there is ocean water, neglecting the elastic effect on land upstream? This choice should be clarified and justified in the text.

The mixture of alpha and w is confusing to me. Line 204 says that alpha is “the mean vertical displacement that can be expected during SAR data acquisition”, but based on units it is the fraction of maximum displacement expected. A clear, physically motivated definition of alpha, with units, would help if placed in 3.1.4. Also, we need a bit more physical explanation about how alpha is determined—in particular, I am not clear on what assumptions about spatial variations are employed here.

Some reorganization of methods and results is needed. Section 4.2 is a confusing mix of methods and results. I am not clear on what these mosaics in Figure 7 are. I am assuming they are DInSAR images aggregated in some way, but it is not clear how. It seems to me that this relates to section 3.1.4, but I am not completely clear. Lines 321 to 326 are methods and so belong under the top-level header of 3.3.3 (this would have helped me understand the motivation of multiple models better there, too).

I would like to see a brief analysis of how thickness errors would affect the results. I assume this is minor, based on how thickness enters Eq 4, but it would be nice to exclude this completely.

Line comments

Figure 2: The scales appear distorted in b (Antarctica is the wrong shape). The axes should be checked so that squares are square.

L209: It is not clear whether the adjusted maps are alpha itself or the DInSAR measurement after adjustment

L230: How does a fulcrum facilitate transmission?

L289: Reduced accuracy makes it sound worse; improvement like this is normally referred to as greater accuracy

L299: “Notoriously” is hyperbolic and unnecessary. Simply remove it.

L305: Not clear what it means to “perform…combination”

Figure 7: Plotting in blue on top of an image with surface meltwater is just confusing. I suggest making the background image black and white throughout

L380: I think this sentence needs rephrasing—does the IBE really do the reduction?

L391: Tide deflection ratio is not defined—is this alpha?

L429: The crystal lattice typically refers to sub-grain structure (i.e., the arrangement of molecules), not the aggregate of grains as used here. Suggest “the polycrystal” instead.

Throughout: hyphens are only used between double nouns when they modify something. So “raise sea level” is correct, as is “sea-level rise,” but it is incorrect to write “raise sea-level.” There are a number of errors in this vein in the manuscript.

This is a really interesting paper doing some innovative things about investigating the spatial variations in effective Young’s modulus near the grounding line that is deeply needed for updating our knowledge about the in situ rheology of ice and tidal processes in the grounding zone. It’s a good site to pick for this analysis to sidestep the firn problem and the grounding line migration. It is excellent technical work at the difficult intersection of models and observations. 

Overall the figures are rich and detailed and could generally be accompanied by a bit more narrative explication. I really appreciate figure 4d, I’ve rarely seen the tidal corrections overlaid like that and it’s but helpful and interesting to look at the relative magnitudes and phases. I think figure 9 i-l tells a good story and is helpful to understanding the method.

Overall, I think the narrative and “thesis” of the paper, and the sequence of what exactly was done, could be made clearer to the reader. Providing a roadmap in the methods section might help. I was surprised when certain aspects of the methods came up, for instance the radar thickness data. For this paper, I would also not assume the reader is at all familiar with alpha maps and elect not to force them to read the preceding paper. A standalone explanation is needed and they can be referred to the previous paper for details.

I also think that some of the modeling choices could be fleshed out in greater detail, particularly the value for the Young’s modulus of ice, and the assumption of an elastic bed with the spring constant used in the work. I know Sayag and Worster (2013) have a value for the spring constant in there and I’m curious how it compares. Sketching some uncertainty bounds around these parameters would strengthen the argument that the signal in the flexure can be distinguished enough from the noise to attribute it to the Young’s modulus of the ice.  

I also think the connection to fabric is somewhat tenuous and might be rebuilt somewhat around the surprising idea that we just don’t know very well what affects Young’s modulus in situ. It may be worth touching some of the older and newer literature around laboratory experiments on the stiffness of ice. I might restructure the discussion to include a general discussion of the main takeaways in the results before getting into the weeds of viscoelasticity that hasn’t been brought up yet (though I understand the need for the justification of the elastic model, which I am fine with). There are some things I found interesting that didn’t get returned to- the shape of the bulge in figure 1e for instance. Overall this makes a clear contribution to the field and will be made even better with a clearer and more self-contained explanation of the methods.

131: Why 1.6? There’s a range found in other studies (mostly not referenced here).

146: I’m curious about what only means here, was there consideration given to changing the boundary conditions?

160: what does “adjustments for the input data used for predictions” mean?

185: this is a bit confusing and could use a more extended discussion in plain language, connecting back to the method at large.

200: From this description I don’t know what an alpha map is, and certainly couldn’t reproduce it from this paper. Even though referencing another paper, a recapitulation here would help, especially as it seems important to the methods of this paper in discerning what we’re comparing.

215: what does “processed the data” mean?

221: sources for k = 5 MPa? My impression is this is very uncertain and probably varies by a lot.

226: first mention of effective Young’s modulus? What are you defining it as in this paper?

245: what was the magnitude of these corrections?

258: I could use another sentence or two on what thickness update means here.

269: I think this is the first mention of radar thickness data, how do you use it?

288: it’s not abundantly clear to me what least squares adjustment means here.

341: why might they over then underestimate? If you discuss later, you can point the reader there. Also, we may want to be careful about prescribing the exact location of the grounding line from interferograms. The extent of upstream flexure is likely past the grounding line because ice is thick.

356: how these statements follow from one another is unclear to me.

Minor comments:

75: sentence fragment

288: “millimeters”