Review paper egusphere-2025-2157

Assessing the Impact of Earth Observation Data-Driven Calibration of the Melting Coefficient on the LISFLOOD Snow Module

By Premier et al.

General Comments

This study investigates the calibration of the snowmelt coefficient in the LISFLOOD hydrological model using Earth Observation (EO)-derived snow cover data. The authors propose two EO-based calibration methods and assess their impact on snow cover fraction (SCF), snow water equivalent (SWE), and discharge simulations across nine European river basins. The manuscript contributes to ongoing efforts to integrate remotely sensed data into large-scale hydrological modeling.

However, several methodological ambiguities, design inconsistencies, and literature gaps limit the manuscript’s clarity, reproducibility, and broader relevance. The introduction focuses heavily on LISFLOOD while neglecting to situate the work within the substantial body of existing literature on EO-based snow calibration and assimilation techniques, many of which have long addressed multi-objective calibration using snow and streamflow data. The authors should better articulate the novelty of their approach beyond its application to LISFLOOD.

This is particularly important given that the improvements achieved with EO-calibrated snowmelt coefficients remain modest, or even questionable, with respect to discharge simulations. This raises broader concerns about the hydrological value and operational significance of the proposed methodology.

Moreover, several critical aspects of the methodology—such as the SWE–SCF parameterization, spatial resolution strategy, calibration procedure, and test basin selection—are poorly explained, inconsistently justified, or insufficiently analyzed. The comparison between models, methods, and performance metrics is often difficult to follow and underinterpreted. Key information for reproducibility (e.g., calibration configurations, data preprocessing protocols) is also lacking.

While the topic is relevant and the integration of EO data into hydrological modeling remains important, the manuscript in its current form suffers from fundamental methodological opacity, weak novelty positioning, and limited hydrological impact. Key sections are unclear or poorly justified, the experimental design is inconsistent, and the results do not support the claimed contributions. For these reasons, I recommend rejection. A revised version would require a substantial restructuring of both the methodology and the scientific framing to meet the standards expected for publication in HESS.

Specific Comments

• L14–15: This sentence is too vague to provide meaningful insight into the methodology or key contributions.
• L15–75: The introduction overfocuses on LISFLOOD and insufficiently addresses broader research on EO-based calibration and snow data assimilation. The authors should frame the novelty of their study in light of widely used multi-objective calibration approaches and explain how their work differs in terms of technique or purpose—not merely model specificity.
• L59–60: The use of snow data in hydrological model calibration is not new and has become a common practice for over a decade. The statement should be revised to reflect this context.
• L66–67: The role of Sentinel-2 data here is unclear. If its main function is downscaling MODIS, this should be stated explicitly. Furthermore, cloud-free MODIS products (e.g., MOD10A1 Version 6) and well-documented gap-filling techniques are already available—please clarify why these were not used or compared.
• L110–115: Calibrating 14 parameters without detailed justification seems excessive. A summary table of parameters and ranges is essential. A sensitivity analysis would help assess the importance of the snowmelt coefficient relative to other parameters and reveal possible interdependencies.
• L111: Please clarify whether model calibration is based solely on streamflow using KGE. If so, this should be justified in light of the study’s stated focus on snow processes.
• L123–124: If all 14 parameters are optimized per sub-basin against streamflow, why isolate the snow module for analysis? The risk of equifinality and parameter interactions should be acknowledged and discussed.
• L137: The description of elevation banding is unclear. How are elevation classes defined and implemented at the 1.4 km model resolution, which significantly smooths real terrain features? What are the implications for snow accumulation and melt representation?
• L140–164: The SWE–SCF parameterization is central but confusing. Equations (7), (8), and (10) appear circular or contradictory. Their derivation, purpose, and assumptions must be clarified. Also, kaccum plays a key role but is not explained. A graphical illustration would help. The brief mention of the Swenson & Lawrence vs. Zaitchik & Rodell methods lacks depth and justification.
• L165: Is the snowmelt factor calibrated independently of other LISFLOOD parameters? If so, a discussion of the implications and potential benefits of multi-objective calibration (including SCA and runoff) is needed.
• L169: The snow balance equation is invalid in glaciated basins where annual melt can exceed snow accumulation due to negative mass balances. The method should either exclude these basins or account for ice dynamics.
• L173–176: The intent of this paragraph is unclear. Please rephrase to clarify what is being estimated or illustrated.
• L178: What is being compared here? A model simulation using observed SCFs? The terminology and structure are confusing and require clarification.
• L165–191 (Section 2.4): This section should be rewritten to clearly explain both EO-based methods for estimating melt factors. The current text lacks transparency and methodological rigor.
• The resolution mismatch between EO data (50–500 m) and model grid (1.4 km) introduces major issues. Downscaling MODIS to 50 m and then reaggregating to 1.4 km is not clearly justified. How are orographic gradients in precipitation and temperature accounted for at this coarse scale? The authors should better discuss whether a semi-distributed approach (e.g., elevation bands) or higher-resolution modeling would improve consistency with EO data and SWE estimates.
• The manuscript suggests the key research question is spatial calibration (pixel vs. basin scale, L47–48), but this is insufficiently explored. How do calibration results differ at each spatial scale? What is gained or lost?
• L202–209 & Table 1: The basin selection lacks justification. Several catchments (e.g., Arve, Salzach) include glaciers, while others (e.g., Guadalfeo) are subject to strong anthropogenic influences (e.g., reservoirs, diversions). These factors are not modeled and introduce significant uncertainty. Their inclusion must be explained and justified—or their results treated with caution.
• Table 1 / Calibration vs. Regionalization: It is unclear why some basins are calibrated while others are regionalized. This methodological inconsistency needs to be explained. Consistent baseline comparisons are essential to interpret calibration effectiveness.
• Figure 1: The coarse DEM resolution leads to incorrect hypsometry (e.g., Arve basin's maximum elevation is ~4800 m a.s.l., not 3700 m). This smoothing likely affects snow (and ice) accumulation and melt modeling and should be discussed.
• L204–209: The temporal alignment of model forcing (1992–2022) and snow data (2017–2023) is confusing. Are independent evaluation years used? If so, how is calibration/control separation ensured? A proper split-sample test would strengthen the study.
• L216 and Throughout: The manuscript uses many overlapping abbreviations for calibration methods (e.g., EO-Cm, EO-Cm1, EO-Cm2, LBFGS-B, L-Cm) with insufficient explanation. This confuses readers. Provide a summary table of methods and a glossary of acronyms. Terms should be redefined when introduced in different sections.
• L220–225: The differences in results across basins should be discussed. Are certain physiographic features (e.g., elevation, land cover, glacier presence) associated with better or worse performance?
• L270: This section is mischaracterized as a “water balance” analysis, but it is actually a comparison of LISFLOOD SWE with other model outputs. The full hydrological balance (precipitation, evapotranspiration, storage changes) is not analyzed, which would be relevant.
• L279–281: Comparing LISFLOOD SWE with other models without harmonized forcing data is misleading. The comparison should be framed as qualitative or exploratory—not as validation.
• Figure 7 and L319 etc.: “Climatology” is misused. Use “seasonal average” or “mean monthly values.” Also, explain what the envelopes in the figure represent. Monthly aggregation may obscure important daily dynamics—consider showing daily averages instead.
• Metrics Reporting: The interpretation of metrics (e.g., RMSE, KGE) lacks depth. What does a specific improvement mean in operational or hydrological terms? A summary table of relative improvements across basins would aid comparison.
• L295–300: This methodological content appears out of place in the results section, indicating a need for clearer structure throughout.
• L325–385: The discussion should better engage with existing literature on snow data assimilation. It is widely recognized that improvements in snow state representation do not always lead to improved streamflow prediction. This should be acknowledged and contextualized.
• L345 & L380: The SWE–SCF conversion is treated superficially. Other formulations exist and should be discussed. Additionally, the distinction between calibration and data assimilation should be made clearer, especially if the authors position their method as a calibration approach.
• Model Structure: The limited impact of improved melt factors on discharge suggests structural limitations in LISFLOOD (e.g., degree-day assumptions, decoupling of snow and runoff). These issues deserve more attention in the discussion.
• L408–409: This conclusion is not strongly supported by the preceding results and should be revised or qualified.

The manuscript would benefit from careful revision for clarity, structure, and language. Sections are often dense and overly technical, with insufficient explanation of key decisions. A clearer narrative structure, consistent terminology, and simplified figures would greatly improve readability.

Premier and colleagues have presented an improved calibration approach for the LISFLOOD snow module that is based on leveraging high resolution satellite data. This approach minimizes the error between observed and simulated snow cover fraction, and directly impacts the simulation of SWE. Authors test this method across a variety of study catchments in Europe and provide a detailed analysis of the improvements in snow simulation, as well as an interesting water balance perspective.

This paper is technically sound, and the effort of using high resolution satellite data into a large scale hydrological model is relevant and interesting for HESS. At the same time, there remain some aspects that could be expanded and improved. I still see value in this manuscript, and thus I am recommending a major revision.

My main point is that using snow data in addition to streamflow data in calibrating a hydrologic model has been widely explored (see for example https://www.tandfonline.com/doi/abs/10.1080/01431161.2010.483493, https://www.sciencedirect.com/science/article/abs/pii/S0022169419312132?via%3Dihub, https://www.sciencedirect.com/science/article/abs/pii/S002216941300320X, https://hess.copernicus.org/articles/26/5627/2022/hess-26-5627-2022.html, https://www.sciencedirect.com/science/article/abs/pii/S0022169424013167). As a result of significant research in the hydrologic community over the last 15 years, a multi-objective calibration that involves at least snow and streamflow data is now considered state of the art. Meanwhile, even doing so does not necessarily imply an improvement in model performance.

This manuscript fits in this state of the art and confirms most of the conclusions above. To me, the most interesting points here are the use of high resolution satellite data and the inclusion of a variety of catchments, with different snow climatologies and various hydrologic characteristics. In the revised manuscript, I would invest more effort in leveraging this variety of cathments as a way to draw process-based conclusions from this study that could allow for generalization: how are these catchments representative of specific snow climates? What do differences in results across these catchments tell us in terms of hydrological processes and the applicability of this approach in ungauged regions?

Authors also consider a fairly long period of data, with several snow drought episodes. Maybe commenting results across extremes and average years could be another way of bringing about more novelty.

The Introduction and the Discussion section could be revised to (1) make the scope of the manuscript broader and (2) discuss how this methodology compares to previous attempts in this realm (see above).

I agree with authors that a calibration in terms of snow cover fraction is currently the only feasible approach at these scales, even though this requires the additional complication of a SCF parametrization to convert modelled SWE into modelled SCF. This is well discussed in the manuscript, with the only recommendation of providing some additional results on the calibration of the k constants.

In general, the manuscript is well written.

Premier et al. present a calibration method for simulating snow melt using the LISFLOOD hydrological model. The authors tested the method on a sufficient number of basins in Europe and demonstrated the benefits for SCF, SWE, and to a lesser extent, for water balance components.

In my view, the paper's novelty lies in the use of improved high-resolution snow cover data, combined with an SWE to SCF approach and an optimization algorithm. It seems to me that the topic is relevant and of interest to the journal, but it requires a major revision.

The paper is missing some points:

It appears that the authors have introduced the SCF calibration as an alternative to the discharge calibration. Stepwise calibration or data assimilation using snow data, soil moisture, and evapotranspiration has been performed quite often in the last decade. Even with the Lisflood model attempts have been made by Thirel et al. (https://www.mdpi.com/2072-4292/5/11/5825, https://www.sciencedirect.com/science/article/pii/S0034425712003604).

The paper does not employ a multistep approach (first snow, second discharge) to improve overall calibration. As mentioned, Lisflood is the driving hydrological model of EFAS and GloFAS, which focus on discharge forecasting. An improvement in SCF is fine, but it cannot be the final goal. An improvement in SCF can even lead to a worse objective criterion of discharge, but might still be an improvement because it reduces the error of overfitting.

Here, the focus is solely on the snow ablation process, using the snow melt coefficient (SMC) as the parameter. The process of snow accumulation, with parameters such as snow factor or temperature threshold that determine whether precipitation falls as rain or snow, is overlooked.

The Lisflood snow modul is not explained fully. It is mentioned that Lisflood uses three different elevation zones (line 134), but it is not explained how the SCF calculation from SWE, the calculation of SMC (e.g., equation 12), or the optimization is performed with these three zones.

Especially with higher resolution (here 1 arcmin) the day-degree approach can accumulate too much snow at high altitudes, as temperatures will not too often drop below 1° C. Lisflood uses a workaround to melt additional snow in Summer (IceMeltS). The paper does not mention this approach, nor does it take it into account.

The effect on the water balance is calculated on a monthly basis, even when the model is run on 6-hour timesteps. Here, it is really necessary to go on daily basis. With monthly evaluations, you miss the main advantage of your SCF calibration: having a better estimate of the timing of the main snow ablation, and therefore a more accurate estimate of the timing and magnitude of spring floods.

The 2^nd step of calibration for discharge is missing, as is an explanation of how to derive a better KGE with a change in SMC. In L_Cm version of Lisflood, SMC is calibrated to improve the KGE (SMC is optimized for discharge KGE). In the EO-Cm version, you changed only the SMC, and you keep all the other calibration parameters? The improvement in KGE (even the tiny one) can only be explained by a bigger range of SMC and/or by the single cell values. However, the calibration was performed on daily discharge; therefore, a comparison with daily values would be appropriate.

A 2^nd discharge calibration is necessary to see the improvement vs the original calibration, using the new SMC as predifined values. I am not asking for all 9 basins but for those where you have only one subbasin (Arve, Laborec, Morrumsan, Umealven)

Specific comments:

• L2: I would not call it traditionally. It is not made because of tradition, but it has a reason. If you call it later traditional calibration, it is ok
• L21: This is unclear. It cannot be globally between 40-90% snow contribution from mountains. Please check Viviroli again
• L25: “LISFLOOD is one of the most comprehensive operational models used in Europe to simulate hydrological processes”. This is very general sentence. Maybe a unique selling point: Lisflood is one of few operational models calibrated for Europe to simulate hydrological processes.
• L34: I think the equation which takes rain into account is from: Speers, D.D., Versteeg, J.D. (1979) Runoff forecasting for reservoir operations - the past and the future. In: Proceedings 52nd Western Snow Conference, 149-156
• L65: for a “novel” method you explain not much in L183-184
• L103: “The current model setup operates …”. Maybe put this after line 106, because the first part explains Lisflood, the second a special application of Lisflood for the EFAS setting
• L131 it is rainfall per day not rainfall intensity. Somewhere else it should be hydrological year instead hydrological season
• L136: The 3 zones can be explained in more detail and has to be included in 2.3 and 2.4.
• Also the IceMelt part in https://github.com/ec-jrc/lisflood-code/ is not explained at all and not taken into account.
• L146ff: This part can be done in a nicer way. E.g. https://egusphere.copernicus.org/preprints/2025/egusphere-2025-1214/egusphere-2025-1214.pdf has a better way to structure this.
• L152: How is kaccum calculated?
• L155: What is the reference of this equation?
• L161: How is this calculated with the 3 elevation zones
• L169f: The equation 11 is invalid for glaciers and cannot applied for areas with always snow and with several snow-cycles. Equa 12 is again without the snow elevation zones.You showed it anyway, that this equation is not leading somewhere. It is fine to keep this approach.
• L183f: You featured this as “novel” approach. It appears to be an optimization for a single-parameter part of the standard SciPy library. Does seem to be novel and not explained at all.
• Table1: the max elevation is not explained. In the original Merrit DEM it is much higher, so I assume you average that for 1 arcmin. But in the model the max elevation is the highest elevation zone. I think you should correct the elevation by the values from original Merrit DEM
• L297ff: Why using a monthly comparison. The original model is calibrated on daily values. The biggest effect of your improvents are the timing in days of the biggest drop in snow accumulation. The comparison to daily discharge is necessary to conclude if the models performance is improved (maybe the over discharge KGE is reduced, but some spring floods are better timed, the snow cover is better estimated).
• Fig 7: Gallego and Guadelfeo have some reservoirs included. It would be better to use subbasins without too much human interference. From the results, you cannot see if it is the snow or the reservoirs. You explained why Guadelfeo has a bad KGE. One solution could be to use only those years without reservoirs,
• Table 4: This is not suitable for comparison. 1) you keep the other parameter constant (I assume, it is missing in the paper) 2) you compare on monthly values 3) you did not recalibrated the other parameters after setting SMC to your values.
• I think it is necessary to re-calibrate for a number of basins (maybe only those where you do not have upstream-downstream calibration) and discuss the effect of your improved SMC e.g. worse KGE but better representation of snow, more exact timing of snow-induced flooding,

Overall, the topic is interesting, and the potential for a good paper is there, but it lacks structure, and fundamental key points are not included yet.