The paper gives a good overview of the operational slushflow regional forecasting system in Norway, which is probably unique in the world. It gives some good background information on slushflows and what kind of situation may lead to slushflow danger in general, based on previous papers on slushflows. The paper is of importance to all who are dealing with this problem,  forecasting for and warning against slushflow danger.

Here are a few questions and/or comments for the authors:

• According to our experience, slushflows can initiate in slopes that are quite steep in general, however the starting point might be in an area with inclination <30°. The starting point can be in a small „step“ in the slope, or at the lower part of a high and steep mountain where the slope starts to ease off. I feel that sometimes, the risk of slushflows may be underestimated in areas where the slope in general is considered to be too steep for slushflows but still includes areas where slushflows can initiate.
• It is mentioned that physical mitigation measures are expensive if possible, and in some areas difficult to implement. Therefore, EWS is important. It is also stated that the initiation of slushflows can be forecasted reasonably well. In my opinion it is important to consider physical mitigation especially in places where slushflows pose serious threat to settlement. There is great uncertainty associated with forecasting the time and location of a slushflow. In some slushflow paths the complication and cost is not as high as for typical dry snow avalanche mitigation measures, but in other areas it is more complicated.
• In Figure 2 (flowchart) the hazard level becomes automatically green (1) if the ground is not frozen, saturated or a bare rock. Earlier in the paper it is, however, stated that requirement of water saturation can also be met with unfrozen ground and when a thick ice layer is covered with snow. Perhaps slushflows occurrences in such conditions are so rare that they are not taken into account?
• In Table 2 it is a bit unclear to me what SD (cm) stands for. Is it the total snowdepth according to a model in Xgeo? Or does „Sum 1-3 Days“ apply to the snowdepth – is it the accumulated snow within the last 3 days? As I understand it, it is the total snowdepth, but then it is assumed that a total snowdepth of 0-25 cm can lead to danger levels 2, 3 and 4.  However, in the flowchart in Figure 2, snowdepth less than 25 cm automatically leads to danger level 1. Does „Sum1-3 Days“ apply to the water supply (rain + snowmelt)?
• It would be interesting to include in the paper a bit more about how well the forecasting system has worked in practice. It is important to look at days both with and without slushflow events and check how often these weather, soil saturation and snow conditions occur, without any slushflows being recorded. I realise it is not easy due to the sparse slushflow data, however, some analyses of this has probably been done in Norway?

It would be interesting to try these methods in Iceland and other countries and continue to improve the system.

Limitations of the scope of the present review

This manuscript has been previously reviewed by Harpa Grímsdóttir and, apparently, revised by the authors. However, the present review refers to the originally submitted version, and I cannot assess to which degree the changes suggested by Harpa Grímsdóttir have been implemented. I am neither actively working on slushflows, nor am I involved in avalanche, landslide or flood-warning. This review will, therefore, focus on the physics aspects of the forecasting methodology, its validation and the way of presenting it to an audience that may be assumed knowledgeable about natural hazards in general but not about slushflows in particular. Numerous minor comments and language suggestions are collected in the annotated manuscript.

General considerations

This manuscript reports on the regional forecasting method for slushflows that has been developed and operated by NVE in Norway for about a decade. This slushflow forecasting service is one-of-a-kind worldwide, and the methodology has not been presented in a peer-reviewed scientific journal before to my knowledge. As such, the topic clearly falls into the scope of NHESS, is novel and will be of interest to the journal’s readers. Moreover, I applaud the authors for publishing an account of their methodology in a scientific journal—it is important that a state-wide service like this be properly documented not only in reports written in Norwegian but also in a form that is accessible to scientists worldwide.

In general, I found the manuscript interesting to read and informative. The comments by Harpa Grímsdóttir are, in my opinion, well taken and should be incorporated in the revised version. In addition, there are three broader aspects—to be explained below—in which I consider improvements highly desirable.

Justification of the methodology

The general flow of the assessment process is explained in Sec. 3.1 and Fig. 2. In that flow chart, there is a big question mark indicating the final decision whether slushflows are consid- ered sufficiently likely to occur in the target region during the forecasting interval to justify issuing a warning at level 2, 3 or 4. Section 3.6 reveals that the criterion for this decision is the ratio of water supply to the snowpack (sum over 1 d or 3 d) to snow depth. This criterion is quantified in Table 2 for the danger levels 2 to 4 and for four different categories of critical snow types. Sections 3.2–3.5 explain how it is assessed whether water infiltration into the ground is impeded or not (Sec. 3.2), how the snow properties and particularly the snow wetness are estimated (Sec. 3.3), how the water supply to the snowpack is modeled (Sec. 3.4) and how information on slushflow occurrence is collected (Sec. 3.5).

As it stands, Section 3 leaves numerous questions unanswered:

1. What is the difference between slushflow danger levels 2, 3 and 4? I suspect they differ with regard to the forecasted number or size of events, but I could not verify this from the text.
2. How do the values stipulated in Table 2 compare to the observations in the slushflow events from which the table is derived? (A plot analogous to Fig. 6 is desirable.)
3. How exactly are observations (or non-observations) of slushflows incorporated into the decision process? The statement at lines 489–490 is fairly vague.
4. Is the regional topography not taken into account at all? At a grid size of 1 km², the gridded hydro-meteorological data do not take into account terrain features at the scales relevant for slushflows. Soil frost, soil saturation and ground water level seem to have the same spatial resolution of 1 km² and would not be sensitive to temperature differences within a grid cell, which can be substantial in high-relief terrain. It is unclear at which resolution liquid water content in the snow is estimated and in which way exactly it affects the estimated slushflow danger. Similar questions concern the water supply, both from rain on snow and snowmelt. One would expect that the type of terrain determines how frequent terrain features are that favor slushflow formation. The latter presumably has an effect on the hazard level that is assigned under given hydro-meteorological conditions. If this factor is not included in the assessment, it is OK, but it would be helpful for the readers if there was an explicit statement of this.
5. Can parts of the analysis process be formulated in mathematically to make their description more precise? I also miss a more general discussion of the pros and cons of different approaches to forecasting slushflows, or at least of the reasons why the ratio of water supply to snow depth should be the most relevant indicator and by itself be sufficient. This question might be discussed on the basis of the hydrological and mechanical mechanisms responsible for slushflow release.

Validation of the methodology

Validation of a regional forecasting method is a crucial yet difficult step because the true hazard level is never known exactly. The manuscript does not carry out a comprehensive validation or at least propose a strategy for doing so. Instead, three slushflow episodes in Norway in 2018, 2021 and 2023 are used to show that slushflow events were expected to occur in all three cases on the basis of the estimated water supply–snow depth ratios. This is a plausibility check but cannot be considered a validation.

Being unfamiliar with the operational aspects of the forecasting service and not knowing the details of the available data sets, I cannot propose a more rigorous validation plan, but perhaps some of the following suggestions could be helpful:

• The sensitivity of the values in Table 2 can be tested by randomly omitting a certain number of cases and recalculating the table. Doing this a sufficient number of times, the standard deviation of the threshold values for all the categories can be estimated.
• With the available data, it ought to be possible to compare the forecasts to the a posteriori assessed slushflow hazard level based on observations and—as importantly—non-observations of slushflows in the different forecasting regions. The uncertainty of the observations can perhaps be accounted for by using fuzzy logic when evaluating true positives vs. true negatives, false positives and false negatives?
• The importance of the human component in the forecasting process can be tested by having different (teams of) forecasters who independently evaluate the data and issue a hazard-level forecast over a sufficiently large number of days.
• The contribution of the complete methodology and particularly of the water supply/ snow depth ratio to the forecasting success can presumably be revealed if the forecasters first assign hazard levels without knowing the WSRs for the different regions (these hazard levels are not to be issued, of course!) and then elaborate the official forecast with the help of the WSRs.

Without at least a valiant attempt at validation, the manuscript remains essentially at the level of a project report rather than being a scientific paper.

Presentation

The authors have undoubtedly given the structuring of the manuscript some thought, with Fig. 2 in Sec. 3.1 showing the workflow and the following subsections detailing the different steps in sequence. In Sec. 3.6, the WSR is introduced and Table 2 presented. Section 4 explains “the human factor” of the methodology and also presents three example cases from Norway. Section 5 gives two examples from outside of Norway, and Sec. 6 looks at the prospects for arriving at statistically derived slushflow threshold values before discussing how the slushflow activity might develop under a changing climate.

This looks fine as an outline, but the text left me a little dissatisfied for the following reasons:

• The two parts of Sec. 4 have little logical connection, the second part would fit much better into Sec. 5.
• Similarly, Sec. 6 contains two disconnected topics. Future developments could be in a final section with conclusions and an outlook, whereas the topic of climate change feels artificially propped onto the paper. The options are to (i) leave it out, (ii) move it into an appendix, or (iii) make it the sole topic of the next-to-last section. The introduction should then, however, clearly motivate why this topic is included in the paper.
• There is a slight incongruence between the steps indicated in Fig. 2 and the sectioning of the text explaining these steps. Evaluation of the WSR could be shown as its own step in Fig. 2, followed by a “synthesis” step. Section 3.5 (observations) does not have a clear counterpart in Fig. 2. The first part of Sec. 4 could become 3.6 or 3.7.
• Even though the introduction and Sec. 2 are not excessively long, they feel lengthy because they contain many details that are not relevant to the main topic (e.g., the matter of run-out modeling, which is largely irrelevant for a regional forecast). Moreover, the text does not get to the heart of the matter before Sec. 3.
• There is no clear rationale stated for why this procedure is the best way of forecasting slushflows. It would also help if the authors stated even more explicitly where subjective assessments enter in the process.

Based on the points above, I recommend to restructure the text along the following lines:

1. Remove all sidetracks or relegate them to appendices, so as to focus more on the core messages. In Sec. 3, there is presently much material that has a certain interest but is not essential to understanding the forecasting procedure. If it is moved further back, the main part of the paper becomes clearer.
2. At the beginning of what presently is Sec. 3, discuss briefly which physical mechanisms must be incorporated in the forecasting procedure, then introduce your procedure with a modified Fig. 2, followed by (more concise) explanations of the single steps. Emphasize which steps are “objective” and where expert judgment enters.
3. The second part of Sec. 4 and the first part of Sec. 5 could be used as examples in a section on validation.

Even though the English is mostly good, the language needs improvement at many places. There are numerous small grammatical errors and formulations that lack precision or (linguistic) logic. Many of these instances are marked in the annotated manuscript.

Recommendation to the editor

The topic of this manuscript fits the scope of NHESS and is of practical relevance in the Nordic countries. While the proposed forecasting method is more empirical than scientific, it can be considered novel. For these reasons I hope the paper will be published in NHESS. Before this, however, the authors should reconsider the structuring. The reasoning that led to this forecasting procedure should be outlined clearly and the crucial step of validation addressed more comprehensively. Finally, the many annotations concerning small issues throughout the manuscript should be addressed (without listing them all in the Reply by the Authors, however!).

In view of the sum of required changes, I recommend encouraging the authors to undertake a major revision of the manuscript.

Oslo, 2023-12-12

Dieter Issler