General comments:

I think that I reviewed this manuscript for another journal, and if so, I was supportive of its publication at that time, and still am.  I do note some relatively minor, but important corrections to the “narrative” being presented, and I describe them now:

The abstract uses the words “miscommunications”, “misinterpretation” and “misconception”.  I think that these words are sort of unfair to the early scientists who developed the initial modes of thinking about, doing analysis with and modeling ice shelves.  These early scientists were well aware of the fact that shear stress in the vertical was prevalent in ice shelves at amplitudes that could be large (e.g., at an ice front or when there are large thickness gradients); however, their intention was to develop strategic simplifications and approximations which would allow glaciological science to make progress.  Their pioneering work leading to the “shallow shelf approximation” was fundamental to the progress of glaciology through the 1960’s onward to the present day.  It is thus not only unfair to their legacy to imply that they were “misleading”, but it is a kind of cheap writer’s trick to introduce the substance of the present paper.  I strongly object to this tone and think that it detracts from the paper by setting up a false “combative” tone that completely misleads the reader.  

I see that this tone that I object to is not present in the Introduction, and the authors very correctly laud the initial development of one of the most effective approximations in glaciological history (the shallow shelf approximation).  This is important. And I compliment the authors for having done so.  But again: I see words like (line 65) “persistent mischaracterizations”.  This is a false and incorrect statement: approximation is not a mischaracterization.  

A challenge:  After recently attending the AGU and also reading a paper by Catherine Walker:

Walker, C. C. and Gardner, A. S. (2019). Evolution of ice shelf rifts: Implications for formation mechanics and morphological controls, Earth and Planetary Science Letters, 526,115764, doi:10.1016/j.epsl.2019.115764.

I became aware of the fact that many rifts on the Antarctic ice shelves are not vertical, but slightly offset from vertical, and that they have an interesting, not-fully-understood asymmetry of the rift shoulders associated with bending moments.  I wonder if this phenomena (also described in one of Walker’s papers on ice shelled planets) is an observable phenomena that is directly related to the subject of this paper.  If the authors think that it is, then they might find that their paper is made even stronger by including references to the Walker study, and also to (not sure if this is as relevant):

Walker, C. C., J. N. Bassis, J. N. and Schmidt, B. E. (2021). Propagation of vertical fractures through planetary ice shells: The role of basal fractures at the ice-ocean interface and proximal cracks. The Planetary Science Journal, Vol. 2, No. 4, doi:10.3847/PSJ/ac01ee.

Specific comments:

line 2 of abstract “…, extending in only one direction,…”. I’m pretty sure that Weertman’s 1957 paper also gives the solution for spreading in two horizontal directions.

I was not able to find other errors or edits to make, and I commend the authors for doing a fine job of proof reading.

The manuscript is concerned with the mathematical modeling of ice shelf flow. In particular, the authors focus on the role of vertical shear in thin-film approximations of the ice flow problem that are valid for the case of negligible basal friction. The authors state that their goal is to clarify what is in their view a misunderstanding in the main stream glaciological literature, i.e., that “it remains common to misinterpret vertical shear stress as typically neglected in current ice shelf modeling studies”.  

As much as I understand that the intention behind this manuscript is constructive, and as much as I share the authors’ opinion that the published literature is somewhat confusing,  I am afraid I have to express a negative opinion about the content and originality of this work. In fact, in my view this problem has been solved already in rigorous mathematical terms in publications concerning the asymptotic structure of the Stokes problem in the limits of thin flows (low aspect ratio) and extensional stresses much larger than the vertical shear stresses. 

Two main strands of research support my statement: Doug MacAyeal’ s seminal shelfy-stream paper (JGR 1989, Large-scale ice flow over a viscous basal sediment: theory and application to Ice Stream B, Antarctica, see model derivation in appendix A), and more recently Schoof and Hindmarsh, 2010 (Thin-Film Flows with Wall Slip: An Asymptotic Analysis of Higher Order Glacier Flow Models https://academic.oup.com/qjmam/article/63/1/73/1843730, esp. sec. 3.4, the limit of  lambda << epsilon). For completeness, and purely as a side note, the only difference between these two derivations being that Schoof and Hindmarsh retain the stress ratio lambda <<1  (see eq. 2.18, lambda is the ratio between shear stress and extensional stress, whereas epsilon<<1 is the aspect ratio, both taken to be small; then lambda<<1 describe the case of ice flow dominated by extensional stresses, as is the case in an ice shelf), whereas  MacAyeal assumes the distinguished limit lambda ~ epsilon^2 with (lambda, epsilon) <<1  (or, in MacAyeal’s notation, epsilon  ~ delta^2), which is one peculiar case of the broader model category obtained in Schoof and Hindmarsh’s more general limit of lambda << epsilon. Yet, despite this minor formal difference, they obtain the same leading-order model, as noted by Schoof and Hindmarsh.

To illustrate my point, I will refer to MacAyeal’s derivation, which is simple and clear; in his derivation, e_{xz}, e_{yz} are the vertical shear stresses therein. I now use epsilon to mean stress ratio, as per MacAyeal’s notation.

The first key point is about the zeroth-order momentum balance: Yes, to leading order the solution reads e_{xz}^{0} = 0, e_{yz}^{0}=0 (eqs. A25 and A26), but all that means, as the derivation clearly explains, is that these stresses are of order epsilon (epsilon being the aspect ratio) compared to the extensional stresses and the lateral shear stress. This is very different from stating that the vertical shear stresses are zero - rather, it only says that extensional stresses are small compared to extensional and lateral shear stresses.  

To find the leading order expressions for the vertical shear stresses, one needs to carry on with the expansions to the next (first) order. As expected,  the order epsilon corrections  e_{xz}^{1}, e_{yz}^{1} appear in the first order (order epsilon) momentum conservation equations (A30 - A31), as they do in the dynamic boundary conditions that determine the horizontal gradients of the ice shelf surface and bottom (A34-A35).

The misconception pointed out by the authors arises, if I understand correctly, by the fact that   thanks to careful algebraic manipulations e_{xz}^{1}, e_{yz}^{1} disappear from the final momentum conservation equations (A 36 and A37) that must be solved to determine e_{xx}^(0), e_{yy}^(0), e_{xy}^(0). Yet, that does not mean that vertical shear stresses are zero - in fact, they can be computed diagnostically by vertical integration of the constitutive relation with appropriate boundary conditions, once the  problem for e_{xx}^(0), e_{yy}^(0), e_{xy}^(0) has been solved. 

It is my view that this work, published over 30 years ago, already clarifies the issue raised by the authors without any possible doubt, while Schoof and Hindmarsh 2010 provide a further generalization. In light of this, it is my opinion that the manuscript as is lacks the level of originality that is required to warrant publication. 

This paper is aiming to clarify to the broader glaociology community some assumptions made in models for ice shelfs, specifically the relation between vertical shearing and surface gradients. I think such a topic/disucssion is welcome, but the presentation of this needs to be improved in order to reach the inteded audience. I suggest the following edits:

1) Formalize the arguments using perturbation expansions and scalings. The vertical shearing is not "absent", it is just of a higher order in the perturbation expansion I presume (i.e. "neglected"). Is it of the same order as the surface gradients perhaps? I recommend connecting your arguments to the analysis by Schoof and Hindmarch (mentioned here by another reviewer).  A large part of the glaciological community is familiar with perturbation expansions and scalings, and for the ones who are not, they could learn it from this paper. As the papers intent seems to be  educate this should fit in well.  You don't need to erase your other arguments, but I recommend adding perturbation expansions as an supporting, more formal, explanation.

2) The exeriment in Figure 2 is  nice but in my opinion it could be made more interesting. For the purpose of showing that this is actually important in real ice shelf simulaitons, I would extend this experiment, make it more realstic - maybe some variation in the ice surface. 

3) Overall it is sometimes a bit unnecessary difficult to follow the derivations, think about if there is a clearer way to present it. Make the two derivations side by side perhaps? 

4) As mentioned by another reviewer, make sure that its not possible to percieve the tone in a bad way, although I am sure this is not the intent. 

Please find attached referee report.