The paper “Thermal diffusivity of permafrost in the Swiss Alps determined from borehole temperature data” by Weber and Cicoira aims at identifying thermal conductivity values from temperature measurements in boreholes. The data basis are temperature time-series of 29 boreholes of the PERMOS network. Three different methods are used to provide ranges of thermal diffusivities at various depths and times of the year for permafrost and non-permafrost sites. The authors argue this approach is highly beneficial for a wide range of applications, including thermal modelling. In addition to that, the authors analyze the temperature time-series to identify fast temperature changes at depth, indicating non-conductive heat transport. For this they use the results from the statistical approach as threshold criteria. They advertise this method as useful tool to identify non-conductive processes.

I do believe the study is relevant. Thermal properties of the ground in permafrost either in mountains or at high and low latitudes are important for thermal modelling, and the identification of non-conductive processes provides information on relevant heat transport processes. Better parameter constraints can reduce equifinality and thus make models more robust. As is, the paper presents a maybe too-broad list of permafrost-related issues before stating that thermal conductivities have not yet been calculated for the relevant boreholes; seemingly leaving the “has not been done yet” as the motivation/aim of the study. I feel the aim should be clearer and directly include the motivation of the tool; the broad range of permafrost topics can be reduced in favor of some directly relevant studies that give some insights in (non-conductive) heat transport and ways to determine it (e.g. Kurylyk and Walvoord, 2021, and references therein).

The methods to determine thermal diffusivity are briefly described with references but no access to the actual code is given. The authors seem to justify this brief description as they do not develop any new modelling approach here but use existing approaches. I do not understand why the code is not made immediately available at this point. I think this would be beneficial to not just check if there is some overseen issue, but more to evaluate and better understand the processing steps, or if there is an opportunity to adjust something (later more on that). The models produce significantly different results (e.g. Fig.3, Fig.4) but the authors present these results multiple times as “well-constrained”. I disagree with this statement and think the reported values are very wide.

The numerical model method is presented as “simple” and without accounting for latent heat nor convection. In the referenced paper (Cicoira, 2019a) I could also not find the actual code. This makes it even more difficult to understand what is going on in the different approaches and why, e.g. certain time steps might not work for some method. I find that the manuscript lacks a satisfying discussion of the different methods upfront and why one might have to expect very different results. A discussion about this is also lacking later on. The authors say that in Figure 3 the results “[…] have a similar course.” This statement is not quantified (e.g. correlation) and I feel that the results have a different progression. I think the results (the differences) are very interesting but this needs much more discussion, and eventually, an explanation. I also did not fully understand why the analytical solution could only be performed at annual scale. I feel this needs clarification.  

Finally, the authors use the statistical model results to test the temperature rates for plausibility, i.e. if the temperature change at a certain depth is exceeding an expected threshold. The threshold is in this case given by the prediction interval of the empirical approach (linear regression model). A temperature change bigger than this threshold would identify a non-conductive process because conduction would be slow. This is shown extensively in figures 7 and 8, and that this identification is consistent with depth.  I feel like it is not necessary to have all the details; more interesting would be an investigation of the actual deviation from the prominent relationships between the temperature rate and the temperature gradient change (middle and right panels in Fig. 8). And why only these dates are identified as non-conductive, when thermal conductivities fluctuate throughout the year (Fig. 3 – 6). I feel like this part is not analyzed and discussed sufficiently.

In summary, I think that the manuscript presents some interesting and relevant aspects about thermal properties of mountain permafrost. However, I feel that neither the introduction, methods, nor the results are currently sufficient to convey the relevant findings consistently.

In the following I list in arbitrary order some of the key aspects I have issues with, and what I would have expected or wished for to address these aspects in more detail.

The authors choose thermal diffusivity as main focus of their study. Thermal diffusivity integrates specific heat and thermal conductivity (Eq. 3 in the manuscript). In thermo(-hydrological) modelling code the latter parameters are often used in the parameterization (e.g. Westermann et al., 2023). As I could not see the code, I am wondering if this parameterization is also used in the mentioned numerical modelling (Cicoira 2019a) and how values are estimated here? How is the composition of the ground parameterized (fraction of ice, water, air, rock), or is this simplified with bulk values? For the analysis of non-conductive heat transport periods, would the parameterization with specific heat and thermal conductivity provide a neat way to check if this could be explained with varying compositions (water/ice) like the authors speculate? Developing a model to do this might be far out of the scope but then I wonder why the authors did not use an existing model like CryoGrid (Westermann et al., 2023) that provides the process representations to achieve this? I do understand that using thermal diffusivity provides a mean to compare the three different approaches, but I do not see that this is “validating”(l 105) the obtained values from the three different methods; maybe they are all “wrong”(as in they would need themselves a correction factor) or only valid for the (maybe not appropriate) applied methods? This would limit these estimates of thermal diffusivity to the application using the exact same methods used to determine them in the first place. Having a model that accounts more comprehensively for the different modes of heat transport (like CryoGrid) could provide 1) the temporal constraints when different modes are occurring, thus allowing to exclude non-conductive periods, and 2) narrow down the thermal diffusivity values (which can still be calculated using the more comprehensive approach) with knowledge about what other processes are affecting these results at different time periods. This could also aid the assumptions about temporal variability in thermal diffusivity due to mobile water (convection). I am not sure about the exact capabilities of e.g. CryoGrid, but I have difficulties accepting the speculations about water movement in permafrost at almost every time of the year (the example in May 2017 excluded) as reason for the variability in estimated thermal diffusivity.

The authors state multiple times that the thermal diffusivity values are well-constrained (lines 9, 68, 205, 303). I do not see this statement supported given the wide ranges obtained through the different methods (Fig. 3 – 6). Using such wide ranges in thermal modelling, proposed as one of the applications for so-derived values, would result in significant differences regarding the thermal state of the ground. The wording needs to be adjusted to reflect this. If there was a more comprehensive model (previous paragraph), there would be a basis to discuss the different value ranges obtained by the different methods with potential recommendations about e.g. when to use or when to not use them. At this moment, I feel that this is not possible because it is unclear which method to trust, and why one would trust a specific method. Maybe this can be resolved (if not using the more comprehensive approach) by providing sufficient details about how the methods work and what their known weaknesses and strengths are. As this is of central importance, I feel this should already be a dedicated part in the introduction and should be elaborated on even more in the methods. I think that the intercomparison of the methods is a great approach, nonetheless. But should they all be given the same weight?

I was wondering about supporting information about the borehole sites that would provide qualitative boundary conditions like active layer depth, temporal permafrost variability, and possibly changes in liquid water content. I believe the PERMOS sites are not just monitored but there are studies using geophysics (Mollaret et al., 2019; 2024; Buckel et al., 2023). These studies should provide (for some sites) specific assessments of for example thawing and thus changes in liquid water content. I believe this could be beneficial in arguing for possible causes in the estimated variabilities. It would also be great to get a short assessment of whether the sites are supporting the 1D approach or if lateral effects are expected that could impact the results.

Minor comments including grammar (I am not native though!):

• Sometimes very long sentences that are difficult to understand (e.g. l31-34). Consider making multiple short sentences where feasible with one clear key point as central message.
• Some language/grammar mistakes that should be eliminated later in the editing phase. Shortening the sentences will probably help dealing with it already.
• Figures show unexplained blue lines (Fig. 2)
• Could testing different upper and lower thermistors (different distances) provide a benefit for the study? Could this help get more stable solutions for the lower thermistors as the gradient is better constrained?
• Line 5: mention also the uncertainties about the ground substrate
• Line 11: “[…] strong spatio-temporal variations [between sites][…]”
• Line 15ff: Too many implications for what the paper presents and too little about shortcomings
• Line 55: the values are not “arbitrary” in Magnin and Marcer
• Line 75: as mentioned earlier, I think it is very beneficial to provide the code immediately
• Line 88: Is it possible to express “perturbation of temperature” more easily understandable?
• Line 97: the variability in the thermal properties is not just dependent on temperature but the composition of the ground
• Line 107: I do not see “validation” but a comparison
• Line 119: Consider reformulating the “day-by-day” part with something like “increments of one day”
• Line 138: unit missing for 0.1
• Line 145ff: The leading term is unclear to me. Maybe this is then leading also to me not understanding why the analytical approach is not applied at higher temporal resolution. Explain this in more detail. Also provide possibly a reference that is less grey literature (Pogliotti 2008).
• Line 158f: Figure reference should be 2a? “significant representativeness” -> significant correlation
• Figure 2: Missing explanation for blue lines
• Line 166: Quantify “similar course” e.g. with pearson correlation
• Line 169: Consider moving speculation without reference to discussion section with proper analysis
• Line 176: Can’t you use different years (with maximum temperature difference) to identify the thermal properties for the deeper parts?
• Line 184: “valid” suggests that these are real thermal properties. Reword to something like “constrained” (from your filtering).
• Line 194: Grammar. Rephrase.
• Line 198: Semantics. “In comparison, distinctly different values were only found […]” . The previous sentence does not suggest that the ordering is based on non-significant statistics.
• Line 201: Calirfy what the small windows are.
• Line 204 ff: Idea: Why not looking at more stable conditions (very cold); would it be possible to constrain the boundary conditions about thermal conductivity better then? No free water/ no thawing / no percolation?
• Line 248: Replace “sensitive” with something like “are subject to” or make sentence active “Rock masses […] experience …”
• Figure 7: what are the arrows? Unclear until Figure 8 that the points are covering each other. Circles might make this clearer. Is the use of colors for the time of year necessary? It invokes an expectation that there will happen something with this information.
• Line 269: What is the zero line? Is the thermal diffusivity not the slope and thus it should be a slope? Please clarify.
• Line 269: “Finally”: Unclear if this is an additional step or the result.
• Line 275: “most likely” is speculation without proof.
• Line 283 ff: A thermal model would probably use existing temperature measurements either for parameter estimation or validation; this would suggest no need for pre-determined parameters that seem highly dependent on the method. It would in return mean that they would not work if the model uses a specific method as the different diffusivity estimates would not work in such a setup. I see only the point for validation given here. I do not see the following (line 285ff) points supported given this previous point of critique.
• Line 285: Unclear reasoning.
• Line 308: I see a problem here that the simplified (no latent heat, no flow) model will always lack behind (be inferior to) existing and seemingly well-working approaches. If the present approach was based on free non-proprietary software, there would be at least a reason for such development. But since it is based on Matlab this is not given.
• Figure A1 caption: The empirical density function is not proof of normality.

Kurylyk, B.L., Walvoord, M.A.: Permafrost Hydrogeology. In: Yang, D., Kane, D.L. (eds) Arctic Hydrology, Permafrost and Ecosystems. Springer, Cham. https://doi.org/10.1007/978-3-030-50930-9_17, 2021.

Westermann, S., Ingeman-Nielsen, T., Scheer, J., Aalstad, K., Aga, J., Chaudhary, N., Etzelmüller, B., Filhol, S., Kääb, A., Renette, C., Schmidt, L. S., Schuler, T. V., Zweigel, R. B., Martin, L., Morard, S., Ben-Asher, M., Angelopoulos, M., Boike, J., Groenke, B., Miesner, F., Nitzbon, J., Overduin, P., Stuenzi, S. M., and Langer, M.: The CryoGrid community model (version 1.0) – a multi-physics toolbox for climate-driven simulations in the terrestrial cryosphere, Geosci. Model Dev., 16, 2607–2647, https://doi.org/10.5194/gmd-16-2607-2023, 2023.

Mollaret, C., Hilbich, C., Pellet, C., Hauck, C., Gluzinski, T., De Mits, E., Maierhofer, T., Lambiel, C., Bast, A., Boaga, J., Flores Orozco, A., Hendricks, H., Kneisel, C., Kunz, J., Morard, S., Pavoni, M., Pfaehler, S., Philips, M., Scandroglio, R., and Scapozza, C. and the Swiss Electrical Database on Permafrost Team: A database integrating the electrical resistivity data of Switzerland for mountain permafrost spatio-temporal characterisation, EGU General Assembly 2024, Vienna, Austria, 14–19 Apr 2024, EGU24-19517, https://doi.org/10.5194/egusphere-egu24-19517, 2024.

Buckel, J., Mudler, J., Gardeweg, R., Hauck, C., Hilbich, C., Frauenfelder, R., Kneisel, C., Buchelt, S., Blöthe, J. H., Hördt, A., and Bücker, M.: Identifying mountain permafrost degradation by repeating historical electrical resistivity tomography (ERT) measurements, The Cryosphere, 17, 2919–2940, https://doi.org/10.5194/tc-17-2919-2023, 2023.

Mollaret, C., Hilbich, C., Pellet, C., Flores-Orozco, A., Delaloye, R., and Hauck, C.: Mountain permafrost degradation documented through a network of permanent electrical resistivity tomography sites, The Cryosphere, 13, 2557–2578, https://doi.org/10.5194/tc-13-2557-2019, 2019.

The manuscript “Thermal diffusivity of permafrost in the Swiss Alps determined from borehole temperature data” by Weber and Cicoira presents evaluations of the thermal diffusivity from the borehole records of the PERMOS network in Switzerland. While the study represents an extensive analysis, I unfortunately cannot recommend it for publication in its current state. In particular, the manuscript falls short with respect to two critical questions, i.e. “is it new,” and “is it true”.

Is it true? The authors use different methods to quantify the thermal diffusivity which is first of all a great approach. However, the results of their two main methods (“statistical” and “numerical”) differ strongly for many of the boreholes, often not even overlapping within the 5-95 percentiles. This means that at least one of the approaches has severe shortcomings, and the authors do not resolve the question which one of the methods to trust (if any). Even in the presented example (Sect. 3.1), the values differ by more than factor 3 (!!), and I cannot see any convincing attempts to explain this. The authors need to look into the reasons for this mismatch and adapt the methods accordingly. They could for example use synthetic data produced by a heat-conduction-only ground thermal model with known thermal diffusivity (with different types of noise/perturbations added) to test the performance of both methods for different situations, e.g. different depths, different diffusivity values, different temperature forcing and different noise/error patterns in the measurements. They could also use simulations from more process-rich permafrost models (GeoTop, GIPL, GeoStudio, CryoGrid, ATS, etc.) to determine how for example ground freezing or vertical changes in thermal conductivity impact the performance of the different methods.

Is it new? The main finding of the study is the diffusivity values, and these are associated with huge uncertainties (see above). So the key question is if these values represent an improvement over the “state-of-the-art”. Given that there are almost no in-situ evaluations of thermal ground properties, it may seem that there is some novelty despite the considerable uncertainty. However, as shown in Table 1, literature values for different ground constituents are available and there are equations/parametrizations that allow deriving the thermal properties of mixed-phase ground materials from these (linear mixing for heat capacity, empirical parameterizations, e.g. Cosenza et al. 2003, for thermal conductivity). They are routinely employed in land surface and numerical permafrost models. These computational approaches feature a significant uncertainty, too, but also here the range of resulting diffusivities is limited. Thus, given the knowledge of typical subsurface compositions and rock types for the individual borehole sites, which range of diffusivities would one get? If the plausible range that the authors can provide with their analysis is even wider than this educated best-guess from the knowledge of subsurface conditions and literature values, I do not see any significant advance over the state-of-the-art. However, by reducing/quantifying the uncertainties of the evaluation (see above) and comparing the results to such independent estimates, the authors could indeed proof the novelty of their work. 

A secondary finding of the study is the possibility to quantify periods of non-conductive heat transfer (Sect. 4.2). However, also here, I am not sure what “new science” we can really learn from this. It is clear that such processes exist and for many of them we even know the role in the permafrost system, e.g. formation of ground ice by infiltrating meltwater in spring. Furthermore, some of these processes can be detected and attributed with much simpler methods, e.g. by identifying a rapid temperature increase towards zero degrees in case of meltwater infiltration and refreezing. The discussion in Sect. 4.2 is too general and does not focus on identifying situation where the authors’ methods could really be used to achieve novel findings. 

Minor comments: 

L. 55: better: “diffusive and stationary models” without phase change of water

L. 55: “arbitrary values” – it is not true that the values used are completely arbitrary, otherwise the model results would generally be nonsense. They are typically derived for example by fitting the model to observations, or using literature values of the thermal properties for the rock at the site, or even just for “rocks in general”. With this, one can generally get within a factor of two or three of the real value, which of course entails a lot of uncertainty, but is far from “arbitrary”.

L. 58: “underlying permafrost” is too unspecific, as permafrost is not a material (for which thermal diffusivities can be assigned), but defined by temperature. At least provide examples of the actual materials.

L. 69: The diffusivity is not a boundary condition, but a parameter.

L. 75: A modelling approach cannot “represent” a diffusivity, it can estimate/yield/compute diffusivity values.

Eq. 1+3+4: Eq. 1+3 are not the real heat conduction equation, but a simplified form for the special case that the thermal conductivity K is constant in space (which would be the correct form of Eq. 4, see comment below). If not (and this is indeed very relevant for permafrost applications), there is an additional term dK/dz dT/dz, and the heat transfer cannot be characterized by a thermal diffusivity alone, but it requires two parameters, the heat capacity and the thermal conductivity. Eq. 1 violates energy conservation if the thermal diffusivity k varies in space! So the correct version of Eq. 4 must be introduced first, and then the simplified forms of Eq. 1 +3 can be  derived.

L. 97 ff: see previous comment, the equation does not work (well) if conductivity changes in space! This must be addressed already here.

Eq. 4: This is closer to the correct general form of the heat conduction equation than Eq. 1/3. However, it is only correct if the heat capacity c is constant in space, which it often is not, especially if there is a transition from ice-rich to ice-poor ground. The correct general form of the heat conduction equation (which is derived from the continuity equation and Fourier’s Law of heat conduction) in one dimension is c(t,z)*dT/dt = d/dz(K(t,z)*dT/dz), and the authors should start their derivation of simplified forms with this one.

L. 120: how is the second derivative calculated? Please provide the equation.

L. 121: this must be dT/dt, not dT/dz

L. 144: RMSE < 0.05K?

L. 144 ff: The analytical solution is for the special case that heat conduction occurs in a semi-infinite halfspace and the upper boundary condition has a sinusoidal temperature. As a result, the temperature variation at each depth is also sinusoidal. Eq. 5 equation should at least be motivated by such considerations, starting again with the heat conduction equation. The second point is how this equation is used in this work, i.e. annual variations are used and not e.g. daily variations for which the method could in principle work just as well (close to the surface). Finally, the reader needs to know how the amplitudes are determined, given that the true temperature signal is generally not fully sinusoidal.

Fig. 2: I don’t understand the additional lines in Fig. 2c, these are runs with different diffusivity values, right? So the model is forced with the 300 and 400cm temperatures, and the 350 cm temperature is used as target for the fit? If the diffusivity is very small (i.e. goes to zero), the modelled 350 cm temperature should just stay at its initial value and not change at all (which one of the lines does). If the diffusivity is very high (i.e. goes to infinity), the modelled 350cm would just be the average between 300 and 400 cm, pretty close to the measurements. But I am not sure how the simulated temperature can overshoot the 400cm sensor, as in several of the lines? In addition, from my experience, this method only produces good results if at least half a period of an oscillation is available and the target timeseries differs significantly from the “high-diffusivity” case for which it is just the weighted mean of the two forcing time series. But exactly this seems to be the case here, so I am a bit sceptic about the results, especially given the fact that the first method produces a completely different value. The minimum in Fig. A2 is not pronounced at all and a whole range of diffusivities seem to fit well. Could that be improved by choosing a longer window? Please provide a quantitative error analysis concerning a) the influence of random fluctuations likely caused by the measurement system, e.g. the zig-zag structures visible at the very beginning of the time series for the middle depth (the remaining RMSE is often caused by these); b) the influence of the depth accuracy of the logger placement, given that the measurements seem to be taken in a moving rock glacier - what if the middle logger was at 356 cm and not 350 cm, how strongly would that change the results? Furthermore, a zoomed in version of Fig. A2 would be great, all the relevant cases are in the bottom where the RMSE is very close to zero.

L. 204 ff: I am missing a clear statement on how to interpret the widely different values obtained from the two approaches. I think this will be next to impossible without at least attempting a quantitative uncertainty assessment for each approach (see for example previous comment). If the condition “conductive heat transfer only, no phase change” is fulfilled, there can be only one value of the diffusivity, which means that at least one of the approaches delivers wrong results. The authors cannot just let both results stand next to each other or merge them into some sort of range. The authors for example write: “ For all 29 PERMOS temperature boreholes, we successfully quantify the thermal diffusivity at different depths…”. What’s the criterion for success? I agree that the methods delivers numbers, but to what extent can the reader trust them? Fig. 5 is clear evidence that “Stat.” on average yields significantly lower values than “Num.” Why is that? If all these values are somehow possible, the thermal diffusivity is quantified within a factor of three to eight in this study (from eyeballing Fig. 5)? Is that really an improvement compared to making an educated guess from the literature values in Table 1!?

L. 225: “…the range of thermal diffusivity values derived with sLRM could successfully be validated with the numerical modeling and the analytical solution (see Fig. 5…” I am struggling to see this in Fig. 5, the approaches often seem to show completely different diffusivities, in many cases more than 100% difference?

L. 271: is simple freezing of water/melting of ice in the rock contained in the definition of a non-conductive heat flux? 

Reference

Cosenza, P., Guérin, R., & Tabbagh, A. (2003). Relationship between thermal conductivity and water content of soils using numerical modelling. European Journal of Soil Science, 54(3), 581-588.