Review of: Snow fracture in relation to slab avalanche release:
critical state for the onset of crack propagation by Gaume et al.
This manuscript describes a numerical model applied to the problem of snow slab avalanche release. A
slab and weak layer assemblage are modeled using the Discrete Element Method, and model experiments
are carried out that create an artificial crack in the weak layer analogous to cutting the weak layer with a
snow saw in the Propagation Saw Test, a common snow stability test. A parametric study is conducted to
determine the sensitivity of different model parameters to the critical cut length at which the slab-weak layer
system fails (specifically, the length at which the system self-propagates). A scaling analysis of the model
results is applied to determine an analytical solution for the critical length, which is then compared with
field data. Compared to an analytical model that only accounts for slab bending over a rigid weak layer (the
“anticrack” model Heierli et al., 2008), this new scaling for the critical cut length agrees much better with
a wide selection of field data, accounting for the possibility of triggering an avalanche from horizontal slopes
(in agreement with the anticrack model) but better accounting for the variation of observed critical lengths
with slope angle. The intuititive result that shorter “cracks” are necessary on steeper slopes to produce an
avalanche is reproduced.
The authors have responded to the two prior reviews, so I will not belabor minor comments that I have
in common with these reviews. I am actually quite impressed with the meticulous and detailed nature
by which the authors have responded to the reviews, and I think that the proposed additions will make a
stronger paper. There are a few areas in which I think the authors have missed the point of comments
made by Reviewer 1, and although they may seem subtle I think they are important. The authors have
gone to great length to defend their numerical model results and setup, but do not seem very receptive
to comments on model design and assumptions that could in fact make the results more compelling (or at
the least address some shortcomings of the approach). Models are always simplified approximations of the
true physical phenomenon of interest. It is not reasonable to expect this (or any other model) to accurately
address every aspect of the problem, but a certain humility is always appropriate when applying a simple
model to explain a complex real-world problem. The results presented in this manuscript certainly represent
a step in the right direction in explaining slab avalanche release, and address shortcomings in existing models,
so these comments are not meant to undercut the important results here. Rather, my hope here is that the
authors take a more constructive approach to the problem, and take to heart the comments made in each
of the reviews in order to demonstrate that improvements can still be made and that the results presented
here do not represent the absolute “truth” that must be defended from here forward (which seems to have
been the unfortunate approach of many “anticrack proponents”).
One of the more important questions that I had in the model results, and that was also raised by both
reviewers, is the discrepancy between the modeled failure envelope and the measurements of Reiweger et al.
(2015) in Figure 3. The modeled failure envelope does not match the experimental envelope very well at all
in my opinion. The qualitative similarity is not itself convincing enough that the modeled slab-weak layer
assemblage is a faithful representation of reality. My impression is that the DEM setup was not initially
targeted to match this failure envelope, but I am confident that it could be with the right combination
of model parameters (there are many free parameters and options to choose from in building this kind of
model, so a failure to reproduce a given feature is more a failure in the modeler than the model). For a model
applied to explain features observed in actual snow stability tests, I would think that a first validation of the
model would be to reproduce more accurately a realistic failure envelope. I would like to see a more thorough
discussion of why the actual failure envelope was not reproduced, and what steps might be taken to build a
better model. Since the bulk of the analysis in the paper is a scaling analysis of the model results, the model
should initially be constructed to be as physically accurate as possible. The experimentally-derived failure
envelope of actual slab-weak layer combinations tested by Reiweger et al. (2015) should be a first validation
test of the model, and I agree with Reviewer 1 that the model seems to quantitatively fail this test.
There is a further subtlety in the failure of the model to reproduce the experimental failure envelope.
Only one of the two experimental failure envelopes of Reiweger et al. (2015) was chosen for comparison, and
that is of the “fast” experiments (that is for experiments with fast loading rates). The slow experiments of
Reiweger et al. (2015) have substantially higher failure loads in pure shear and pure compression, and thus
this failure envelope is even further from the modeled envelope. It is very important to discuss which of
the two envelopes is appropriate for the rate at which stress is applied in the Propagation Saw Test, and
thus the numerical experiments. The stress rate in the weak layer of the present numerical experiments
should be reported to justify which envelope is more appropriate. I am not convinced that the fast tests are
the appropriate benchmark. Snow is a very rate-sensitive material, so it is a bit disingenuous to report the
experimental results from only one rate without any discussion of why this was chosen. I would be inclined
to believe that the PST falls somewhere between the two envelopes in terms of loading rate. If this is indeed
the case, the modeled failure envelope is even further from the truth (which further calls into doubt the
subsequent scaling analysis of the model results in the paper).
Comment/Answer M1, Reviewer 1: I think this is an important, albeit subtle point here. I’m not sure
that the reviewer’s comment should be dismissed so easily. Many believe that “cracks” are pre-existing
flaws or statistically weaker zones in the weak layer that exist a-priori. Whether enlarged solely due
to gravity or due to an overload, they must exist in the first place. Indeed, in the parlance of fracture
mechanics, all flaws are pre-existing features in a material. One does not create a crack; rather, one
enlarges existing cracks by applying stresses. Of course, when dealing with a highly porous material
like snow, even the definition of what exactly is a crack is an open question. However, it is reasonable
to suggest (as the reviewer seems to imply) that there must be some pre-existing flaw in the weak layer
in order to use the terminology of fracture mechanics and crack propagation. Although you equate
“failure” with “crack” the two are not strictly equivalent in mechanics. There are numerous failure
mechanisms in materials and structures that do not require cracks.
Comment/Answer M8, Reviewer 1 (also M22): This point about whether the shear stress was for
the slab-weak layer interface or some average over the weak layer was made numerous times by this
reviewer, and I had similar comments in reviewing the manuscript before I looked at the comments of
the other reviewers. The authors seemed to interpret this comment as a neglect of the density of the
weak layer, but this actually misses the point (and the fact that this assumption “is usually made in the
avalanche community” is not a logical justification). The stress as defined in the manuscript is indeed
only appropriate at the slab-weak layer interface, which is why the reviewer took this interpretation in
reading the manuscript. In a layered or graded material, the shear stress can change discontinuously
(or at least non-monotically) at interfaces with distinct changes in material properties (like Young’s
modulus). For example, consult the results of (Monti et al., 2016, e.g. Figure 5), in which a simplified
approach is taken for accounting for the multi-layered nature of stresses in a snowpack (of which
several of the authors on this manuscript are also co-authors). Although the results in this paper are
considering a line load applied to the surface of the snow, the gravitational stress calculation used
in this manuscript is only appropriate in a static sense, and the experiments detailed here are strictly
not static. Although I do not believe it is necessary here to re-formulate the shear stress calculation,
the authors should acknowledge that the shear stress for an anisotropic weak layer, with distinctly
different properties than the slab, should not be expected to be uniform throughout the layer. It would
be more appropriate to say something like “we assume that the shear stress acting in the weak layer
is equivalent to the gravitational stress acting at the slab-weak layer interface, i.e. $\tau_g=\rho g D sin(\Psi)$.
Comment/Answer M10, Reviewer 1: I believe the reviewer here was questioning how well your numerical bi-axial tests for characterizing the macroscopic Young’s modulus compare with a relation like
Scapozza’s (Eq. 5 in this paper). I think this is a worthwhile question to answer, as I wonder the same.
Comment/Answer M27, Reviewer 1: It’s kind of a straw-man argument here to apply a theory for a
beam cantilevered over a rigid foundation. If you apply a simple theory for a beam bending over an
elastic foundation (e.g. take the simplest approximation, the Winkler foundation), then the stresses
and deflections depend on both the elastic properties of the slab and weak layer. If the point is to
compare against the anticrack model, which assumes a rigid foundation, then this is not a problem.
However, here you are arguing why this scaling relation is inappropriate for your results, which do
not have a rigid weak layer. I think you would do much better with a more appropriate beam scaling
theory here, and this may not lead to the conclusion (which you state as very important) that the
length scale $\Lambda$ must be used.
Figure 6 In the caption, it is clear that the regression through the new model results was performed without
an intercept (zero-order) term, whereas the intercept was included for the anticrack model (which indeed
seems necessary given the lack of fit). However, it would be more appropriate to perform the regression
through your results also including an intercept, and report the intercept and p-value (which would
likely confirm that the intercept is not statistically significant, but would be a more objective stance
to take for confirming your model results). A confidence interval on your slope term would also be
helpful to report, as it would more quantitatively demonstrate the degree of agreement of your model.
Line 251 Per comments above, I would disagree with the statement that the modeled failure envelope is
“in line with recent laboratory experiments.”
Line 274 Same as above, “realistic” failure envelope is a stretch...
Application To Simulated Snow Stratigraphy: I agree with Reviewer 2 that this section seems out of
context in this paper. It’s a nice sales pitch that this new approach is implemented in this operational
model, but it doesn’t really fit otherwise.
References
Heierli, J., P. Gumbsch, and M. Zaiser (2008), Anticrack nucleation as triggering mechanism for snow slab
avalanches, Science, 321 (5886), 240–243, doi:10.1126/science.1153948.
Monti, F., J. Gaume, A. van Herwijnen, and J. Schweizer (2016), Snow instability evaluation: calculating the
skier-induced stress in a multi-layered snowpack, Natural Hazards and Earth System Sciences,
16, 775-788, doi:10.5194/nhess-16-775-2016.
Reiweger, I., J. Gaume, and J. Schweizer (2015), A new mixed-mode failure criterion for weak snowpack
layers, Geophysical Research Letters, doi:10.1002/2014GL062780. |
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