Dear authors,

The topic is highly relevant for avalanche forecasting and aims to bridge microstructural physics with operational snowpack models. In particular, the analysis of the CT dataset is valuable and extensive, contributing to an improved understanding of how microstructural properties relate to macroscopic properties.

However, the manuscript currently suffers from conceptual inconsistencies, unclear physical interpretation, and methodological gaps that limit the strength of its conclusions.

1. Critical energy release rate vs. critical crack length

From a fracture mechanics perspective, it remains unclear what is meant by the term “critical crack length.” One could interpret it as the finite crack size required for the onset of crack propagation within a coupled criterion framework (Leguillon, https://doi.org/10.1016/S0997-7538(01)01184-6), but this is not the case here. Renaming this quantity to “critical cut length” would help avoid this ambiguity.

Furthermore, the manuscript neglects the second condition required for fracture initiation, namely that the stress must exceed the strength of the weak layer (Leguillon). The context of coupled criteria is therefore missing. 

“The stability of a snowpack and the critical length above which a crack spontaneously propagates depend on both the fracture energy of the weak layer w_f and on the mechanical behavior of the overlying slab”. What critical length is ment here, the finite length of a coupled criterion which needs to be exceeded (like everyone with a mechanical background reads) or the “critical crack length” of a PST (like snow practitioners reads it) ?

“The fracture energy itself is known to be a function of the snow layer density and microstructure”. This has never been stated in the mentioned reference Adam et al., https://doi.org/10.1038/s41467-024-51491-7 

The magnitude of the “critical crack length” derived from a PST does not provide direct information about crack propagation propensity. It is a geometric measure rather than a material property. For the same weak layer, different critical cut lengths can be obtained depending on slope inclination, slab stratification, and cutting direction (see Adam et al., https://doi.org/10.1038/s41467-024-51491-7).

"A small a_c means that the weak layer below the slab is prone to crack propagation.” This statement is incorrect.  A small “critical crack length”  is not a direct indicator that the weak layer is prone to crack propagation, but a configuration-dependent system response of the slab–weak layer–geometry setup as you partly mention: “The critical crack length ac thus depends on both how the slab deforms when it loses support from the weak layer, and the specific fracture energy of the weak layer “. Same applies for “Finally, we examine the potential of predicted critical crack lengths to discriminate between weak layers and more stable layers within a profile.” 

The “critical crack length" has so many geometric and material dependencies which scale differently that its nearly impossible to interpret it. E.g. a longer “crack length” can be related to a stiffer slab due to a crust and even though the weak layer might be potentially dangerous. Vice versa how should be the small “crack length” at lower slab height be interpreted in Figure 9 without knowledge? Those interactions makes the interpretation highly complex, particularly for operational applications or practitioners.

The profiles in Figure 9 mainly reflect the effect of slab stiffness, which causes the “critical crack length” to increase more or less linearly with depth. The observed discontinuities are introduced by the min-cut parameterization associated with different grain types. If the min-cut parameterization were plotted with the corresponding calculated critical energy release rates, this would contain essentially the same information but would be easier to interpret. In this context, the level of “critical cut length” is unnecessary. These values are absolute and configuration-dependent, and therefore not intrinsic material properties. As such, they are not suitable quantities to describe or predict fracture initiation or propagation.

The terminology “crack propagation propensity” is vague. The critical energy release rate describes fracture initiation (or “onset,” as stated in the title). If crack propagation itself is to be addressed, a steady-state framework (e.g., Rosendahl et al., https://doi.org/10.5194/nhess-25-1975-2025) or dynamic fracture processes (e.g., Bergfeld et al., https://doi.org/10.5194/nhess-23-293-2023) must be considered. From a fracture mechanics standpoint, the PST-derived “critical crack length” is not a valid indicator of crack propagation and has historically been misinterpreted in the snow science community.

Since PST measurements are partly conducted on inclined slopes, the relative contributions of mode I and mode II should also be clarified. A brief statement quantifying that the loading is predominantly mode I (e.g., ~95%) and that the analysis is therefore restricted to mode I-driven initiation would improve clarity.

2. Missing physical justification of the min-cut → fracture energy link

No direct experimental validation is provided to support a correlation between min-cut and critical energy release rate.

The argumentation of the parameterization follows an indirect route via the “critical crack length.” The comparison with a constant energy release rate primarily shows that, within the PST dataset, the inferred energy release rate is not constant but varies, likely with density. Since density is also a primary input to the min-cut formulation, the resulting improvement in modelled “critical crack length” does not constitute a robust justification for a physically meaningful parameterization between min-cut and fracture energy.

Rather, this highlights the need for a controlled experimental campaign combining fracture mechanical field tests with direct CT measurements across different grain types.

The correlation on which the parameterization is based remains only moderate.

 It is unclear whether the PST dataset alone is suitable to validate such a relationship across different grain types. It should first be demonstrated that grain types can be statistically correlated with fracture energy derived from the PST dataset itself. If this is not possible, the dataset may not be appropriate for validating the proposed parameterization.

In addition, it is unclear whether the PST dataset contains a sufficient diversity of grain types to support such validation.

The assumption of a fixed weak-layer thickness in the PST analysis is not explained, as this information is available in the original dataset. Similarly, the weak-layer elasticity is parameterized via density relationships derived for general snow types rather than specifically for weak layers. It is not stated which parametrisation is chosen (AC, CT, SMP) from Gerling 2017. This would improve clarity. Furthermore, density-based parameterizations reflect an apparent stiffness rather than the theoretical Young’s modulus. Consequently, the experimental method used to derive such parameterizations should be consistent with the actual loading conditions, particularly with respect to strain rate and time-dependent behavior. For example, formulations such as Gerling (2017) may yield Young’s modulus values several times higher than the effective modulus relevant for PST-type configurations (see Schöttner et al., 2025, Fig. 13a). In addition, more appropriate parameterizations exist for specific weak layer grain types (e.g., Schöttner et al., 2025). A clear separation between the derivation of weak layer and slab elastic moduli is necessary.

Since the weak-layer Young’s modulus strongly influences the calculated energy release rate (see sensitivity study Adam et al., https://doi.org/10.1038/s41467-024-51491-7), it is important to assess whether the observed correlation between min-cut and fracture energy isn’t in fact primarily a density correlation. Given the multiple sources of uncertainty in deriving fracture energy from PSTs, this should be explicitly tested. For example, a direct comparison between weak-layer density and min-cut may already yield similar or even stronger correlations.

The manuscript itself acknowledges that density is the main variable controlling min-cut and that measured densities exhibit strong scatter: ” Since the density of the weak layer is the main variable used to estimate the min-cut in the parameterization Eq. 5,” and “we assume that the min-cut can be related to a macroscopic quantity, in particular the snow density.” A sensitivity analysis quantifying this effect would therefore be highly valuable.

While the min-cut may indeed be a promising proxy for fracture energy, the current approach does not convincingly demonstrate this. It would be more straightforward to directly test correlations between fracture energy and other available microstructural descriptors (e.g., from CROCUS or grain-type parameterizations) rather than introducing an additional layer of assumptions via min-cut.

3. Further comments

• The inclusion of the Heierli model does not add clear value to the manuscript. The WEAC model is state-of-the-art and computationally efficient, and the comparison does not contribute significantly to the overall argument.
• Figure 1 is misleading, as the slab is not represented as a true Timoshenko beam; the boundary conditions do not allow for rotational freedom at the slab end.
• The nomenclature should be used consistently (e.g., a_c vs. AC in figures). Indexing of Units should also be checked carefully m^2 “squared” instead of just m2.
• Introduced variables should appear consistently in figure labels (e.g., min-cut with ζ).
• Figure 5 contains redundant labeling (headers and x-axis labels).
• Figures 3 and 4 appear redundant; one should be removed. Additionally, labeling inconsistencies (“min min-cut” vs. “min-cut”) should be corrected.
• Avoid using red and green with identical marker shapes due to accessibility concerns.
• Use consistent terminology throughout (e.g., “min-cut” vs. “mincut”).
• A schematic overview of the full methodology (similar to Mayer et al., 2023, Fig. 1 https://doi.org/10.5194/nhess-23-3445-2023) would greatly improve readability.
• The treatment of sphericity and SSA is difficult to follow. It is only briefly mentioned in a figure caption (Fig. 6) and appendix. A1 clearer methodological description of how different grain types are handled is needed.
• Key contextual explanations currently presented in the first section of the discussion should be moved to the methods, this would help to better follow the conceptual idea.
• Figure 2 would benefit from additional labelling of the weak layer of interest
• 3.2.2 (Fig. 6Y) ? 
• Figure 7: Indicate clearer within the plots that a) b) are observed and c) d) are simulated. This can only be know with reading the caption. 
• Figure 6 c) to f) x axis label is missing or can not be required to be transferred by the reader from g)  because its another scale and plot. 
• Figure 6: what are the units for time ?
• The inconsistency in error use and their origin is confusing think about adding errors in the whole model chain as well. 
• Figure 7 a) where does the different errors measured for a_c come from? They are rather relativ nor absolute. 

The general approach of estimating the resistance of each snow layer against crack propagation using snowpack models such as Crocus, which resolve microstructural properties, is very promising.

However:

a) The methodological justification of the min-cut parameterization for fracture energy is currently insufficient.

b) The use of the geometrical measure “critical crack length” introduces conceptual ambiguity and reinforces a historically misinterpreted quantity in the snow science community.

A more appropriate framework would directly assess, for each layer, how the available energy release compares to the intrinsic fracture toughness of that layer. This ultimately calls for a physically consistent approach in which fracture toughness is determined through controlled fracture experiments across different grain types combined with direct CT measurements.

Community Comment

As an operational avalanche forecaster and part-time researcher with some experience in snowpack modeling, avalanche release research, and avalanche hazard assessment, I offer the following perspective on this manuscript and the associated public discussion.

Overall assessment

This paper addresses a genuine and longstanding gap: the weak-layer fracture energy w_f has remained a poorly constrained free parameter in crack-propagation models, typically back-calculated from PST data rather than independently estimated from snowpack state variables. The proposed parameterization,  linking w_f to density, grain sphericity, and SSA through a min-cut proxy derived from X-ray microtomography, is a meaningful step toward making crack propagation indicators fully prognostic from snowpack model outputs. From a practitioner's standpoint, programs already running Crocus or SNOWPACK operationally can implement this with modest effort and obtain more physically consistent crack-propagation estimates than a constant w_f provides. That is a real and useful contribution. Beyond its immediate application to crack-propagation onset, the continuously applicable w_f parameterization developed here serves as a foundational input for future work on dynamic crack propagation and fracture arrest at the slope scale. Coupling spatially varying w_f fields derived from distributed snowpack simulations to dynamic propagation frameworks would be a natural and productive next step, crucial to operational avalanche programs, and this paper removes a key obstacle to that work.

On the nature of a_c

The public discussion has generated considerable debate over whether the critical crack length a_c is a valid indicator of crack-propagation propensity. We want to be precise here. Calling a_c a "geometrical measure" understates its physical content; it integrates slab density, elastic modulus, height, weak layer fracture energy, slope angle, and cutting direction through a mechanical model. It is more accurately described as a system property: a configuration-dependent indicator of the onset of propagation for a given slab-weak layer configuration. I agree with the second reviewer's framing, and the impact pressure analogy is apt. Recent work by Adam et al. (2024) and Bergfeld et al. (2025) makes explicit that PST-derived critical cut lengths are not transferable across experimental configurations and that they are most appropriately used to infer material properties, such as fracture toughness, rather than treated as portable physical properties themselves. The paper should reflect this framing consistently.

That said, the configuration-dependence of a_c does raise a legitimate methodological concern that the paper should address more explicitly. Comparing a_c values across different snowpack configurations without adequately controlling for the dominant non-w_f drivers, primarily slab density and height, makes it difficult to isolate the contribution of the w_f parameterization. The slab stiffness gradient with depth dominates the profile-wide a_c signal in Figure 9, and the cross-sectional comparison in Figure 7 conflates variance from slab properties with variance from w_f. The more controlled and compelling validation is actually the temporal evolution analysis in Figure 8, where the same weak layer is tracked through a season with consistently modeled slab evolution. This result deserves greater prominence: it is both scientifically cleaner and directly relevant to operational use, where practitioners need to track weak-layer stabilization over a season.

On the completeness of the physical framework

The first public comment implies that the absence of a coupled stress-energy initiation criterion represents a fundamental conceptual gap. I disagree with this framing. Avalanche release is a chain of distinct necessary conditions: failure initiation, onset of crack propagation, dynamic crack propagation across the slope, crown fracture, and slab sliding. This paper addresses one link in that chain. No single contribution is expected to resolve the full sequence, and evaluating this paper against that standard is not appropriate. The relevant avalanche mechanics literature, including Reuter and Schweizer (2018), has explicitly separated failure initiation from crack propagation propensity precisely because these are distinct problems requiring distinct treatments.

It is equally important to distinguish the onset of crack propagation, which this paper models, from sustained dynamic propagation and fracture arrest, which are mechanically distinct subsequent stages. Bergfeld et al. (2023) separately quantify dynamic fracture and compaction following onset, while Rosendahl et al. (2025) show that slab touchdown can reduce the energy release rate after onset and contribute to crack arrest. The paper's title appropriately limits scope to the onset, but several passages broaden the interpretation toward general crack-propagation propensity and operational hazard monitoring. The claims should be narrowed accordingly: this is a promising parameterization for onset models, not yet a complete description of crack propagation or release probability.

The practical implication is not that the paper's output is invalid; rather, it is that a_c should be interpreted in combination with failure initiation indicators, which is already standard practice in operational programs that use multiple stability indices. A weak layer with low a_c but low failure initiation likelihood is not operationally dangerous, and practitioners understand this. The paper acknowledges this briefly but could be more explicit about it as an operational caveat.

Scientific concerns worth addressing

Setting aside the conceptual debate, several methodological concerns merit attention.

The most significant is the potential circularity between calibration and evaluation. The Richter et al. (2019) PST dataset is used both to establish the linear w_f-to-min-cut relationship and to evaluate how well the resulting parameterization predicts a_c. The demonstrated improvement over a constant w_f is at least partially guaranteed by construction. A leave-one-weak-layer-out, leave-one-season-out, or leave-one-site-out cross-validation would materially strengthen the validation. This matters especially because the performance gain in the operationally relevant Crocus case, the configuration closest to actual forecasting use, is modest: R = 0.76 versus 0.73 and RMSE 10.1 versus 11.1 cm compared to constant w_f. The larger gains appear in the observed-profile case, which is less operationally relevant. The paper should be transparent about this asymmetry rather than leading with the more favorable numbers.

The question of whether the min-cut is doing genuinely independent work beyond density deserves a direct test. The paper itself acknowledges that density is the primary driver of min-cut, and density also enters the WEAC model through the Gerling elastic modulus formulation at a steep power law (ρ^5.13). Without a density-only baseline, and ideally a density-plus-discrete-grain-type baseline, it is impossible to quantify the contribution of the morphology term, as measured by sphericity and SSA. The current comparison with only a constant w_f is necessary but insufficient to support the paper's main claim.

A related concern is mode mixity. The manuscript states that WEAC accounts for mixed-mode conditions, but the inversion setup uses upslope PST cuts, no touchdown, and a fixed weak layer height of 3 cm. Adam et al. (2024) show that fracture toughness is substantially larger in shear than in collapse, and that the historical PST literature contains almost no mode-II-rich data. As currently formulated, w_f looks more like an effective PST-based fracture parameter for a mode-I-dominated loading regime than a general weak-layer fracture energy law. The authors should report the mode-I/mode-II share of the energy release rate for the inverted WEAC cases and explain explicitly why a scalar w_f is acceptable for this dataset and its intended application.

A more technical concern relates to the fitted percolation threshold ϕ_t = 0.04, corresponding to a density of approximately 37 kg/m³. The dataset does not include samples with ϕ < approximately 0.08 (~75 kg/m³ for precipitation particles), so this parameter is extrapolated below the calibration data range. The physical interpretation of a percolation threshold for ice bond network connectivity in very low-density fresh snow is not straightforward, and to my knowledge, the appropriate literature, modern snow micro-tomography work on structural connectivity, does not clearly support a value this low. The sensitivity of the parameterization to this fitted threshold should be reported, and its physical basis discussed more carefully.

The finding that modeled Crocus profiles outperform directly observed profiles is operationally encouraging but deserves careful interpretation alongside the known density bias in Crocus (systematic underestimation of slab density, RMSE 58.8 kg/m³). The authors suggest this reflects measurement noise in density cutters, which is plausible. However, it also reflects that the parameterization was calibrated within Crocus's representational space, where density, SSA, and sphericity evolve with internal consistency. The possibility that the parameterization is better tuned to the model world than to physical reality should be acknowledged explicitly.

From a practitioner and operational perspective

Both Crocus and SNOWPACK have known limitations in representing actual snowpack states, density biases, sensitivity of weak layer formation to temperature-gradient parameterization, and layering resolution constraints. These challenges are larger in many operational contexts than the specific gap this paper addresses. But that context favors this paper's contribution: it removes one source of indeterminacy in the crack-propagation modeling chain without requiring new field measurements or model restructuring.

The validation dataset being drawn entirely from two instrumented research sites 3 km apart above Davos, dominated by DH and FC grain types in an Alpine climate regime, limits statements about portability. The single surface hoar layer in the dataset was not reproduced by Crocus, and Adam et al. (2024) derived their mixed-mode interaction law specifically on surface hoar weak layers, while Schöttner et al. (2026) report distinct scaling behavior across FC/DH, DF/RG, and surface hoar categories. What the paper supports most defensibly is an effective parameterization for PST-onset calculations in persistent FC/DH-type weak layers under the specific modeling assumptions used. The conclusions should reflect this scope rather than claiming generality across snow fracture energy broadly. Maritime snowpacks and thin continental snowpacks are unrepresented, and portability to other climate regimes is an important open question that should be stated explicitly as a priority for future work.

A subtler but equally important limitation is that neither of these study sites, nor most sites where operational snowpack models are routinely validated, are located in actual avalanche start zones. Snowpack models are typically run at weather station sites on flat or low-angle terrain, and their outputs are extrapolated to release zone terrain. The snowpack in a 35-40° start zone differs from a research plot in its wind redistribution history, slope-parallel settlement, radiation geometry, and spatial variability. Whether the parameterization behaves consistently when applied to start zone terrain, where the slab-weak layer system properties are what actually matter for avalanche release, has not been investigated. This is a recognized gap across the broader snowpack modeling literature, not specific to this paper, but it deserves explicit acknowledgment in the context of operational claims.

Conclusion

This paper makes a genuine and implementable contribution to operational avalanche forecasting. It narrows a specific gap, the w_f free parameter problem, that has limited the utility of crack propagation indicators in operational snowpack modeling. The scope is best understood as an effective parameterization for PST-based onset calculations in persistent FC/DH weak layers, rather than a general snow fracture energy law, and the conclusions and title should reflect this more carefully. The public debate around the paper has, in places, conflated legitimate methodological concerns with broader disciplinary arguments about fracture mechanics frameworks that do not directly bear on the paper's contribution. The second reviewer's careful response to these comments is well-reasoned, and I support its framing.

With revisions addressing the calibration circularity, the density-alone and density-plus-grain-type baselines, the mode mixity characterization, the percolation threshold extrapolation, the modest performance gain in the operationally relevant Crocus case, and clearer framing of w_f as an effective PST-based parameter rather than an intrinsic material property, this paper would represent a meaningful and operationally relevant advance.

Thank you,

Ron Simenhois

Dear authors, reviewers, and members of the discussion,

After reading the subsequent reviews and community comments, I would like to add a short follow-up reflection regarding my earlier community comment.

First, I would like to apologize for the tone of some parts of my original comment. I am very engaged in this topic and probably approached the discussion too narrowly from within my own research perspective. In doing so, I expressed some points more harshly than intended. This was never meant as a personal criticism of the authors or to diminish the value and ambition of the paper itself, which addresses an important and timely problem for avalanche forecasting and snowpack modeling.

I especially appreciated reading the later reviews and discussion contributions. In particular, Johan Gaume’s review helped broaden my perspective regarding the interpretation and role of critical crack length approaches and the diversity of mechanically consistent frameworks that can be used to describe propagation onset. I realize that I framed some aspects too strongly around one specific fracture-mechanics interpretation, while the operational and systems-level perspective emphasized by Johan is equally important and valuable in this context. Ron Simenhois also raised several very good points regarding the practical and operational relevance of configuration-dependent indicators such as (a_c), as well as the importance of distinguishing between methodological limitations and the actual usefulness of simplified operational models.

I still believe that some of the conceptual clarifications discussed throughout the review process, particularly regarding the interpretation of (a_c), the scope of the parameterized (w_f), and the distinction between onset and sustained propagation, are important and will strengthen the manuscript. However, I also recognize that my original wording at times overstated the level of controversy around these topics and did not sufficiently acknowledge the broader context and history of avalanche mechanics research.

Overall, I very much enjoyed reading the different reviews and the discussion taking place around this manuscript. The discussion itself highlights how relevant and active this research direction currently is, and in my opinion it clearly underscores the need for such approaches and continued development in this field.

I believe the manuscript is promising and worth publication after revision, although of course I am only a community commenter and not in the position to make editorial judgments.

I thank the authors, reviewers, and community contributors for the thoughtful discussion. I will also take this as a reminder to check my tone a bit more carefully before posting future comments. My intention was always to contribute constructively to the discussion, even if my enthusiasm for the topic came across more strongly than intended.

Best regards,

Valentin Adam