Authors presented results of a novel modeling approach for simulation of isochronal surfaces in an ice sheet model.  General modeling methodology was described in detail in earlier papers of the authors (Born, 2017; Born and Robinson, 2021). The essence of the methodology is the description of an emerging of an isochronous surface and its evolution through time in a host model generated velocity field. In some sense it resembles tracking passive tracers though the body of an ice sheet. Compared to the previous studies (Clarke and Marshall, 2002; Clarke et al., 2005; Lhomme et al., 2005), where semi-Lagrangian approach is implemented for particle tracing, authors use straightforward tracing (so to say, “pure” Lagrangian approach). The novelty compared to (Rybak and Huybrechts, 2003) is that the whole isochronous surface is tracked, not individual particles.

As was mentioned above, the paper is a continuation of the previous studies. From this point of view, it has a more technical focus rather than the research one, though some results concerning evolution of isochronous surfaces through glacial cycles have certain scientific value. Anyway, systematic detailed narration of the method presented in the paper is of course handful and corresponds to the scope of the Geoscientific Model Development.   

Though the authors stress (lines 184-185) that their main goal is not to reach as much closer fit to what they call “observations”, but rather to present capabilities of the method, I would suggest to enlarge the section 3.1 and discuss the problem of distortion and overturning of ice layers close to bottom (NEEM community members, 2013; fig. 13 in (MacGregor et al., 2015)). In view of the severe problems close to the bottom of the ice sheet, the choice of the 115 ka isochrone as target one in the model tests looks ret very reliable and must be additionally justified.

For me, it is not clear how authors technically deal with the lateral ice melting and calving in terms of isochronous surfaces propagation, as well as with changes in ice sheet configuration (retreat-advance) and with basal melting. I suggest to discuss this issue in the revised manuscript.

Particular notes

Line 16: I suggest to add a reference to (EPICA community members, 2006).

Line 16: “ice core data are limited to specific locations”. This is not exactly correct. Because of ice flow, ice core data characterize climate change in the past on a relatively big territory – the deeper is the layer in the ice core the more remote is the place of origin of the ice (see eg. (Huybrechts et. al, 2007 in Climate of the Past; EPICA Community members, 2006, in Nature – specifically, Supplementary materials; NEEM community members, 2013, in Nature; Huybrechts et al., 2009, in Annals of Glaciology). I suggest to add a paragraph discussing the problem.

Line 57: The description is somewhat vague – how can the vertical axis be defined in time RATHER than in space? Either in time or in space, I think, and not a little bit here and a little bit there. In the previous papers (Born, 2017; Born and Robinson, 2021) this issue is enlightened rather clear. I suggest to describe vertical discretization in the more clear way as well as propagation of the isochrone surfaces (layers) in the horizontal (in the vertical, too) in the more clear way.

Line 134: Authors use Shapiro and Ritzwoller (2004) geothermal heat flux (GHF) field to calculate basal melting. Though the GHF field in the cited work seems to correctly reproduce the reality in general, I am not sure about the North-Western Greenland around stations NEEM and especially NorthGRIP, where the bottom layers older than 120-124 ka BP disappeared because of relatively high basal melting rate probably caused by locally enhanced GHF.   

Caption to Fig. 2. Authors use term “observed” for the OIB data which is comfusing. In lines 151-162 authors describe how the OIB chronology was derived as a combination of radiostratigraphy and ice core dating (which is model derived in deeper layers).    

Figure 2, panels a-c: the difference in depth between modelled and the OIB isochrones is confusing, especially if we consider not very “old” ages – 11,7 and 29 ka BB isochrones. These results must be explained and discussed, because the discrepancy in estimates may question the possibility of practical implementation of the method. In this view, I do not agree with the authors (Lines 162-166) that the model reproduces radiostratigraphy “reasonably well”. For instance, in panel b, isochrones 11,7 ka (“observed”) and 29 ka (modelled) merge. Same for 29 ka and 57 ka. I cannot qualify this result as “reasonably well” even taking into account uncertainty in “observed” values.

This paper concerns what I’d describe as a performance tradeoff analysis of a presently unique model (ELSA) that cleverly couples offline with a full ice-sheet model (Yelmo) to generate the resulting synthetic age structure of the ice sheet. The model described is appealingly simple and so the number of model parameters is small, but they are all fairly considered in terms of their impact on the output. The result is a compact study that mostly stands on its merits but could use better context with what has preceded it. I have mostly glaciological and non-modeler type concerns about the paper as it stands. I’ve noted one bigger issue on which that I think the paper needs substantially more clarity for its intended audience.

Major concern:

It took a careful reading and checking of references for me to understand (or think I do) how ELSA vertically advects the age structure and thins the layers at each time step. At first, I was surprised not to see any mention of *vertical* velocities in Figure 1. I wondered if ELSA used a Nye sandwich model throughout the ice sheet, which would not be good. Then I realized that the vertical velocities must simply be determined by continuity from the host model’s 3-D horizontal velocity field. That’s fine, but not expressed clearly in the paper. However, I then became curious about the nature of the host model itself and found that it uses a depth-averaged approximation of vertical shear in the ice column (129-130). While substantial and informative work has been done on this model’s properties (Born and Robinson, 2021; Robinson et al., 2022), I find this an odd choice in the context of resolving the 3-D age structure of an ice sheet as it forces a pre-determined vertical velocity pattern (if not magnitude) on the ice sheet, which is a risk considering past observations (Fahnestock et al., 2001, 10.1126/science.1065370). A potential resolution here would be greater clarity in the model description as to what happens to the isochronal layers *inside* the ice sheet at each time step (not just the top and bottom), and later a more robust discussion of better ways to model an age structure generally. The latter part tends more toward the host model physics and other inputs, so maybe a summary of the conclusions of Born and Robinson (2021) is appropriate.

1: Is it correct to describe this paper as “Introducing ELSA v2.0…”, given the verbiage on L41? That suggests that Born and Robinson (2021) “introduced” ELSA v2.0. This paper still stands on its own merits and is certainly a more complete description. I wonder if a different title is more appropriate, e.g., “Design and performance of ELSA v2.0…”.

23: Is the reference to “Standard tools” those for glaciology or a different field? More context here is appropriate before the relevant citations later on in this paragraph.

132: Clarify what a “sigma-coordinate grid” is for non-modelers. Also, how are they different from “zeta levels” mentioned later on (L203)?

144: Which “bed properties”? There are several relevant ones.

148 and elsewhere: For paleoclimate in much more common usage these days is the use of Common Era (CE) instead of AD for historical ages.

151: There is also pre-OIB data used by MacGregor et al. (2015).

178: parameterization

186: If there’s no section 3.2, then there doesn’t need to be a section 3.1. Also, this sub-section may be more appropriate for the Discussion.

191: I’m familiar with BedMachine and haven’t heard of v3.1. It’s not mentioned in Morlighem et al. (2017), which is simply described as v3. Regardless, BedMachine v5 has been out since mid-2022. I realize that big ice-sheet models are strangely slow at updating their boundary conditions, hence the use of Shapiro and Ritzwoller (2004…20 years ago…) for geothermal flux, but some clarity or nomenclature adjustment is needed here.

204: vertical dimension

263: I’m not knowledgeable in these matters or what GMD policy is, but more commonly whenever runtimes are mentioned or compared I’ve also seen the processor / # cores / etc. described.

Figure 2e-l/3/5/7/A1: Could some colors be added other than gray to distinguish between the ocean, land and ice where the isochrones are not mapped? It’s a bit drab as is with just the present-day coastline.