Review of tc-2023-35 (Wang et al., 2023)

General comments:

The paper provides an assessment of the distribution of ice that meets the targets of the International Partnerships in Ice Core Science “Oldest Ice Challenge" using a kinematic approach inverting observed englacial isochrons dated using an ice core pinning point for the deep age structure of the ice sheet.  This 1-D approach (specifically IsoInv) has been primarily used for the Dome C region, and stands in contrast to 1D thermodynamic approaches that balance both mass and heat through latent heat (eg van Liefferinge et al., 2014, 2018), and 3D full stokes modeling.  The approaches are complementary, with their strengths and weaknesses - thermodynamic approaches have to deal with the tremendous uncertainty in the value of geothermal heat flux, while attaining the deep dated isochrons needed for IsoInv is fraught and the computational cost and rheological and boundary condition uncertainties for 3D approaches limit their usefulness.

This paper represents an overall readable contribution to the literature on old ice distribution modeling.  I don't have fundamental problems with the conclusion.  Aspects of the presentation and discussion would benefit from being made clearer.

Major points:  

Gray literature: The paper does lean on preprints somewhat.  The study by Chung et al., submitted is obviously highly coupled with many of the same authors - one would anticipate that the methods this paper refers to will not change greatly, but there is a risk.  A larger issue is the pointers to the preprint by Obase et al. 2022, looking at complementary thermodynamic modeling where the reviews indicate that there was an error in the calculation of the basal thermal gradient.  Presumably this is addressed in the final accepted (but not yet published) version of that paper.  While the Obase paper is obviously very complementary, the Wang paper should either drop the explicit comparisons, or at least provide some caveats on that comparison.

Figures:  The maps are hard to read, especially at printed scale.  I recommend removing the greyscale DEM bed elevation background and using some well spaced contours instead in a different color than the surface contours.  Increasing the plotted point size of the data point may also help make the ideas conveyed more visible.  The authors discuss specific candidate old ice sites in the text - they should indicate them on at least one of the maps.  The indicators for DF and NDF are hard to make out at printed scale. More specific points are below.

Flank flow versus divide flow:  1-D models are really only appropriate where ice velocities are very low, as the authors point out, but the case they make for Dome F could be made better.  They use the statistical spread of basal ice ages as a function of distance from key Dome points as an indicator for flank flow, but don't make their logic clear on why that should be the case. Isn't this statistical trend just a fractal distribution as you cover more and more area with expanding range from the dome?  A map of ice flow velocity, or an indication of ice velocity on the maps would be helpful.

Age uncertainties of internal reflection horizons:  This was confusing.  How are depth uncertainty, range precision and best guess uncertainty combined?  Is range precision actually calculated from using the SNR? If so, where are the results (which should be different for each IRH).

Stagnant Ice:  At Dome C the stagnant layer has a distinctive radar character.  The authors should comment either if similar features are seen at Dome Fuji, or if the radars that have been used can even detect it.

Specific points:

Abstract line 6: probably best to use 'basal unit' to replace 'basal layer' following on Lilien et al., 2021.

Line 26: replace 'feasible' with 'useful'

Lines 37-39:  The Bo 2014 paper, with the 3-D model, is more of a point to the issue discussed above - they conclude that "Hence, with the observations available now, we cannot constrain the age of the basal ice well.".  The 1.5 million year where the ice is not melting from their Figure 6 is an assumption used to drive their model thermodynamics, not a result.

Lines 40-: the paragraph starting at line 40 is very long and dense and could be broken up.

Line 56: "on an airborne radar surveys" should be "on airborne radar surveys" or "on an airborne radar survey".

Line 89: what is a 'two-dimension filter'?

Line 98: "in all survey lines, the third IRH H3 is" change to "in all survey lines, however the third IRH H3 is"

Line 128: "The estimate of the range precision is always higher than the resolution" - the numerical value for precision should be smaller than the resolution for a well behaved echo waveform; I would not use the term "larger" to mean "better".  maybe finer verse courser?

Line 264: for lazy readers who skip the methods, I would add "We show the reliability index (described in section 2.4)"

Data availability: It would be good to get the IRH data at least in a repository prior to acceptance.  Technical issues with getting the radar data are more understandable, but we should as a community be moving toward getting that as well. For the ice thickness product used for the modeling, would it be more appropriate to point to the Eisen et al., 2020 (https://doi.org/10.1594/PANGAEA.920234) product for the line based data?

Figure 1: While Greene et al., 2017 should be cited if AMT was used for these plots, Greene et al is not an appropriate citation for the surface elevation data.  AMT provides at least 3 different surface DEMs for Antarctica, and this paper should reference the one ultimately used.

Figure 2: what is the strong line at ~250 m depth?

Figure 5: gray polygons (the Van Liefferinge et al., 2018 data) on a gray scale map does not work well

Figure 6: the patches of blue stagnant ice are nearly invisible in this rendition. It might be better to have a separate figure or indicate existence rather than thickness.  The distribution with respect to lakes you have here is interesting with comparison to Dome C where we apparently have lakes under stagnant ice.

Figure 7: it's very hard to tell what is going on with the overlapping color zones.  Especially if one is color blind - STD and Run III could look identical.

Review of “Mapping age and basal conditions of ice in the Dome Fuji region, Antarctica, by combining radar internal layer stratigraphy and flow modeling”

This manuscript seeks to map out properties of the ice near the bed around Dome Fuji, East Antarctica. The authors trace layers in an airborne radar survey from 2017/2018, and date those layers using the age scale from an ice core drilled at Dome Fuji proper. They then fit a 1D pseudo-steady model (that has been applied extensively to Dome C) to the isochrones at each trace in the radar survey, from which they get an average accumulation, shape factor, and effective ice thickness (indicating stagnant ice or basal melting) at that point. The results suggest very old ice in the area, albeit with enormous (and, according to the authors, underestimated) uncertainty.

In the end, the conclusions here are rather thin. The issue with taking the method of Chung et al., in review, and using it on this survey is that the isochrones used here are much less than half as old (170 ka vs 476 ka), and the resultant impact on the reliability of the results is enormous. Essentially, the issue is that a 170 ka isochrone tells us very little about 1.5 Ma ice. Multiple problems can occur: small violations in model assumptions will result in inferred ages that are unrelated to reality (e.g. if ice flow, ice thickness, or accumulation varied in unexpected ways), and overfitting to measurement errors on these young isochrones will cause incorrect results at older ages. Indeed, when the authors check this possibility with even a 230 ka isochrone, they find that there is a huge change in ages as we would expect if the young isochrones simply do not carry much information about deeper ages. In my view, that this problem is occurring is demonstrated conclusively since the model does not match the Dome Fuji ice core’s age scale. This is the only really available test of the model reliability—and not only does the model miss the age scale, but it does so outside its reported uncertainty! That is to say, the model is both wrong and confidently so. As a result, I do not think that much can be concluded from this paper, other than that old ice may or may not exist at Dome F. To their credit, the authors describe the limitations in the discussion and conclusion (though it should be better disclosed in the results), so I think that after revision the work will be publishable in The Crysosphere.

I think the presentation could be improved in both the paragraph-scale structure and at the sentence level, and the figures could be improved as well. The paper is in need of quite a bit of grammatical work, as there are a lot of missing or extra articles and some subject/verb mismatch. I did not enumerate these in my review. At times I found the paper hard to read, although I think I could eventually discern the meaning, so this could probably be handled by a copy editor. At some points, paragraphs wander away from the thread of the manuscript (see general comments). I agree with the other reviewer that the figures are pretty difficult to make out given their size. Throughout the manuscript, colorbars start and end at arbitrary values and demarcations are difficult to read—well chosen start and end values, arrows to indicate whether the colorbar values are inclusive, and enlargement would help.

General comments

Basal layer is a sticky term. As used on line 26, it sounds like generic deep ice. However, in other literature, it refers specifically to ice that has a distinct radar character, to the ice near the bottom of EDC that has little discernible paleoclimatic information, or to ice that is inferred to be stagnant. The situation is further muddled on line 70, where the authors suggest that their method can detect a potentially stagnant basal layer—but this is incorrect. The method can only detect a stagnant basal layer (at least in terms of vertical velocity), since the whole premise of the detection is that the basal layer is stationary for the purposes of the depth-age scale. This work should be consistent on its usage of the term basal layer and it should define what it means by that in the introduction. Imprecise usages such as that in line 26 should be removed. Some discussion should be added on whether there is any correspondence between the areas where stagnant ice is inferred and any characteristic of the radargrams.

Given the wide pulses of this radar system, and the lack of pulse decompression, I am skeptical of the vertical precision that the authors are claiming and I would suspect a bias. Just by two way travel time, the pulse is 50 m long (as the authors correctly point out, this is the resolution, defined here as the separation needed to identify two targets as distinct). Again, as the authors correctly identify, this resolution is different than the precision (i.e. the depth-accuracy of a target). However, the authors trace in a fairly standard manner (picking the strongest return), but given the processing of these data the depth of the reflector should really be off the first return, assuming that time zero is defined as the start of the pulse (indeed, this is what you would get if you could do pulse decompression). The problem is that I would expect the strongest return to lie below the first return from a reflector (most likely 25 m below, but this offset is somewhat arbitrary), but never above. Thus, I think that there is likely a systematic bias in the ages and depths used. This may have a small effect on age-depth scales in the end, since it may affect an isochrone in the same manner along its length, but it should be accounted for carefully.

Overall, uncertainty deserves a more prominent place in the results and discussion. First, how is the basal age uncertainty that the authors report calculated? I am guessing it is as in Chung et al., but there is not even a passing mention in this manuscript of how the authors obtain anything other than a best-fit value—it is critical to add this to the manuscript. Then, there is the issue of uncertainty in basal age ice—the number reported for Dome F itself is plus minus 500 kyr. This is enormous, over a third of the age. Figure 4 should plot the uncertainty on the basal ages—without this, the reader has no idea if there are any areas at all with reliably old ages. This gets addressed later by table 1 and the sensitivity analysis, but I see no reason that it cannot fit in Figure 4.

The comparison with Karlsson 2018 and van Liefferinge 2018 deserves more consideration. While the approaches are different, what can we learn by comparing them? Where should we believe their results over the results here (for example, are the results here thermodynamically tenable)? Where is there agreement?

The introduction could use some work. We would benefit from more focus on what the reader should take away. This is most obvious in the paragraph beginning at line 40 wanders between detailed analysis of timescales, studies that concluded something about basal thermal state and potential old ice sites (without ever stating those conclusions). I suggest a careful culling of the introduction, focusing on the goals of each paragraph.

Detailed comments

L36: If efforts beyond BE-OI are discussed, it seems strange to include Dome A but not other countries’ oldest ice efforts. For example, Beem et al. (2021) would then also be appropriate here. Also on L36, the sentence needs to be rephrased—is the point that the age is limited or that it reaches 1.5 Ma?

L81: I find this system description to be a bit vague. I was under the impression that the AWI system is multi-channel and phase-coherent. Is this a single channel power, or the total transmit power? Pulse-limited is not a term we see that often for ice-penetrating radars (perhaps more for radar altimeters), so it would be helpful to say the importance explicitly—that it acts much like a chirp system where you cannot decompress the chirps (thus the very low vertical resolution). Is there no reported bandwidth because there was no frequency sweep in the chirp? If the chirp did sweep frequencies, the bandwidth should be reported.

L89: Should explicitly state what kind of 2d filter

Figure 1: “examplary” implies that it is an ideal or “the best” profile, while I think simply “example” would be more accurate. Different colors for contours and survey would help readabilility. An increase in size would be nice too.

Figure 2: The horizontal black lines make this almost impossible to interpret. I would also like to see a zoom in on some of the tracing, so that we can see how the traced depth relates to the width of the returns. Why not just use a plus/minus for the uncertainty and avoid the confusing double parenthetical?

L140: This needs to state how accumulation is inferred for ages that predate the oldest ice in the core

L141: “Inverted” means “was turned upside down”--but this was both inverted and integrated. Here “inferred” or simply “calculated” would be correct.

L142: This needs to be rephrased to make clear that the presence of stagnant ice is undetermined

L149: Considering that Chung et al. And Lilien et al. use inverse methods that produce uncertainties, it is important to state here whether this method does the same or whether this work simply finds the single solution with the lowest misfit.

L156: Could this be renamed? It is essentially the inverse of the reliability, so it is quite confusing to call it the reliability index.

3.1: Same issue with meaning of “exemplary”

L171: Delete parenthetical—thickness cannot be deep

Figure 5: The Van Liefferinge data need a different color—gray on a gray background is unreadable.

Final paragraph: I do not think this is a conclusion, nor is it a logical way to approach the limitations of this work. Overall, it is a rather weak note to end on—why not move it to the discussion, which is what it really is anyway?

References