the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
| 29 Jan 2024
A numerical study of process complexity in permafrost-dominated regions
Abstract. Numerical modeling of permafrost requires adequate representation of atmospheric and surface processes, a reasonable parameter estimation strategy, and site-specific model development. The three main research objectives of the study are: (i) to propose a methodology that determines the required level of surface process complexity of permafrost models, (ii) to design and compare different conceptual numerical models of increasing surface process complexity, and (iii) to calibrate and validate the numerical models setup at the Yakou catchment on the Qinghai-Tibet Plateau. Three cases with varying top boundary conditions have been established: (i) Case 1: Dirichlet thermal boundary condition of measured surface temperature at 0.0 m. (ii) Case 2: Surface water and energy balance without snow. (iii) Case 3: Surface water and energy balance with snow. The calibration was carried out by coupling the Advanced Terrestrial Simulator (Numerical model) and PEST (Calibration tool). Simulation results showed that (i) Permeability and Van Genuchten alpha of peat and mineral were highly sensitive. (ii) The thawing of permafrost was not adequately represented by considering only subsurface processes. (iii) Liquid precipitation aided in increasing the rate of permafrost degradation. (iv) Deposition of snow insulated the subsurface during the thaw initiation period. We have successfully established a pseudo-1-D model at the Yakou catchment in the Qinghai-Tibet Plateau. A novel methodology is proposed to assess the surface process level complexity in permafrost-dominated regions. The numerical model can be used to determine the impacts of climate change on permafrost degradation.
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RC1: 'Comment on egusphere-2023-3122', Anonymous Referee #1, 01 Mar 2024
The presented manuscript presents a substantial volume of work performed however several major aspects of the presented study significantly reduce its quality and value.
1. Though the manuscript states a goal of establishing surface process complexity -- the cases that are supposed to represent different levels of said complexity are unrealistic and unjustified. No contemporary hydrological/coupled heat and moisture transfer model is forced with only Dirichlet conditions for surface temperature. This forcing can be imagined for models where no moisture transport is present (f.e. GIPL, some versions of CryGrid), however, these models are calibrated using a cost function that solely depends on soil temperature. Case 2 in that sense is even more odd since snow is universally represented in any model that is concerned with heat and water balance.
2. The spinup procedure in the presented study differs from commonly used ones (e.g. Evans and Ge, 2017; Lamontagne-Halle et al., 2018; Debolskiy et al., 2021). For scenario 0, it is unclear what the temperature or energy flux boundary condition at the top of the domain is set to (L135 only states "initial temperature"). The "freezing from the bottom" approach is unrealistic since in situ soil freezes only from the top.
3. Calibration procedure: It is not quite clear why a single objective function is used in this study for optimization. PEST software tool pwtadj1 calculates weights for observational groups based on contributions of the observational groups to the objective function and its derivatives. This approach is not particularly useful in the case of temperature and volumetric water content since these variables have different parameter sensitivity rankings. Moreover, Case 1 (for which, unfortunately, no mass top boundary conditions are presented in the manuscript) should not be calibrated with a cost function containing soil moisture. The model will try to compensate for the inadequate boundary conditions with calibrated parameters which is f.e. evident in the residuals histograms and figure 7. Instead, it would be more beneficial to run a multi-objective optimization algorithm (PEST software should have this capability), maybe with a metaheuristic such as Particle Swarm optimization, Differential Evolution (f.e. NSGA-II), etc. I would encourage the authors to compare the results between the calibration done with MOO and their results in the manuscript.
3.1 The authors do not consider the uncertainty in the observations to which the model is calibrated to. F.e. "volumetric water content" (which I assume is volumetric liquid water content) measured by DTS and FDR sensors under sub-freezing temperatures is subject to higher uncertainty than under positive temperatures thus former observations have to contribute less to the cost-function value.
3.2. Reduction of the parameter set for calibration. It is not quite clear how 21 parameters have been reduced from case 1 calibration to case 2 and case 3 calibration when in Table 4 all three cases have differences in calibrated parameter values in 18 out of 21 parameters. Moreover, in Table A1 only 9 parameters have bounds values for cases 2 and 3. Further comparing Tables 4 and A1 it is clear that a lot of calibrated parameters for different cases have values at the bounds or close to them. This further indicates that the calibration procedure needs more careful consideration from the authors.
Minor remarks:
1. Table 1 needs a rework since it is really hard to understand. In text (L140), there are only scenarios I,II and III mentioned.
2. Figure 4, Even with the current opacity it's hard to see all three cases's residuals. Consider making them line graphs instead or separating them into 6 subplots.
3. Table 4 and Figure 5. One of them is redundant.
4. Figure 6. Plotting RMSE and mean bias with depth would be much more illustrative than NSE.
5. Whenever the temperature is being ploted - it's benefitial to have 0 degree line to visually separate thawing/freezing. Also, figures like Figure 7 would benefit from having monthly ticks on x axis with months labeled instead of number of days.
Citation: https://doi.org/10.5194/egusphere-2023-3122-RC1 -
RC2: 'Comment on egusphere-2023-3122', Anonymous Referee #2, 15 Mar 2024
The authors investigate in the article the capability of a model implemented with an existing code (Advanced Terrestrial Simulator) to reproduce date from the Quinghai-Tibet Plateau (QTP) with three different upper boundary conditions. After a short description of the model (with slightly more information in the appendix), the calculation of the initial condition with a spinup phase and of calibration and validation, they shortly introduce the location and topography of the experimental site and finally present the results of the calibration process where the quality is measured by the residual as well as the nash-sutcliffe efficency (NSE) coeffient. Finally they compare the simulated temperature and volumetric water content with averaged experimental values and present results for energy and water fluxes at the surface.The paper is well written and the language is adequate. However, I have some major issues with the paper:
- First of all, there is major information missing. I did not find anywhere in the paper, how much snow there is on the surface of the experimental site and for which period of time. While there are plots about precipitation and snow fall rate in the appendix, they are in the rather unhelpful unit of m/s instead of mm/day and there is no information about yearly rainfal or snow water equivalent (only mean annual precipitation). This is an essential question for assessing, what upper boundary condition is reasonable. Still, according to the data in figure A1 and the mean annual precipitation of 405 mm given in section 2.5 this is not a dessert spot. Therefore, I do not see, why the authors assume that their case 1 scenario with only a prescribed surface temperature and no water input at all should result in a reasonable result (it does not as the NSE in figure 6 shows).
- According to section 2.5 the slope in the up-slope region, for which the numerical model was developed, is about 20 degrees. Therefore in the nearly saturated conditions when the active layer is thawed (with a volumetric water content of close to 40 percent) significant lateral flow is to be expected. This can not be handled by a one-dimensional model and might also be a reason for the extremely poor NSE in the lower part of the profile.
- There is very little data available to determine the huge amount of parameters (12 to 21 of the model). The authors write that "the number of observations greatly surpasses the number of parameters", but this is not really true. Most of the year the moisture content is either close to zero or close to saturation. The only information is in the time during which the transition occurs. The temperature at lower depth is also strongly smoothed, so there is also much less information than the number of days suggests. This should be taken into account in the calibration as well as in the assessment of the quality of the agreement. One of the central questions the paper needs to answer would rather be: Can a physically based model be calibrated with so little information?
- According to line 473-484 of the appendix the authors assume that during melting the density of snow is constant. However, everybody who has ever been outside in snow knows that there is a settling process. As a consequence the density of fresh powder snow is much lower than the density of a snow crust. This wrong assumption might result in major errors in the upper boundary condition.
- In their final simulations the authors compare the simulation results to experimental values averaged over several yearly cycles. However, the laws of physics refer to actual properties. As the processes in permafrost are highly non-linear, the averaged values will most certainly not be described by the same physical laws. Thus the comparison is meaningless.
- I find the histogram plots of residuals not helpful at all. They give no insight, where or when discrepancies are large or small. This would be necessary information, because it is relevant, if the model only matches the easy to catch phase during winter well, when everything is frozen or if it also is a good representation of the dynamic time during freeze and thaw. Besides, the box plot makes a comparison of the scenarios impossible. Points or lines would have been much better.
- Finally, the results obtained in the paper provide very little new insight into permafrost dynamics in general or in permafrost on the QTP in particular. Basically, an extremly simplified model (only temperature) gives very poor results. More realistic models are better, but with as little data, they still give poor results.
Although the paper is well written, I propose to reject it based on the stated problems of the approach taken and because of the lack of new scientific insight.Citation: https://doi.org/10.5194/egusphere-2023-3122-RC2 -
RC3: 'Comment on egusphere-2023-3122', Anonymous Referee #3, 24 Mar 2024
This paper applies the numerical ATS code coupled with the PEST calibration tool to compare different levels of complexity for representing the top boundary condition of a 1D freeze/thaw system.
Three cases are compared: a fixed surface T, and heat balance conditions with and without snow cover.
The paper is well written but needs clarifying and correcting; see comment below and in attached copy. Figures are clear and well-prepared. References are good. The methodology is justified.
The comparison confirms some previous published results including high sensitivity to near-surface parameters. Some other interesting explanations for sensitivities are also provided.
It is not clear how or if parameter interdependence (correlation) was accounted for. This could be an issue with so many parameters used for calibration.
There are issues in comparing these different scenarios.
I didn’t see any estimates of uncertainty or error in the input data used for calibration.
In Case 1, the proximity of the Dirichlet BC to the observed data seems an issue.
Specific comments:
- ‘mineral’ is used throughout the text to describe the subsurface layer below the peat. This is confusing especially when referring to parameters, as its not always clear if the authors mean the solid (mineral) phase or the bulk porous medium. Needs clarifying. Should be replaced with ex.: ‘soil’ or ‘sediments’. Check for clarity in parameters for this layer – if they assume dry or saturated conditions.
- L40: These are only the processes included here, they are not all processes as implied in the sentence. Similarly, L42: these are not the ‘main’ processes’, what about flow ? Needs rewording.
- L50: ‘to prevent cold air temperatures from reaching the subsurface’ needs rewriting. Yes, this is the net visible result, but of course heat can only flow from hot to cold so the process is the opposite: should say something more like ‘it prevents heat in the subsurface from escaping’.
- L54: ‘The degree of surface process complexity is determined by the climatic conditions in the study area.’… needs rewriting. The degree of simplicity/complexity depends on the applied modelling approach.
- L57-58 seems inconsistent. In one sentence conduction is said to (always) be dominant, in the next groundwater inflow is mentioned as being important.
- Fig 4: Case 1 residuals are not visible, I assume they are hidden behind the others ? Should bring them to front.
- Table 4 & 5… 5-6 digits is excessive precision. 3 digits is plenty.
- Eq 1: I couldn’t find the actual values of the objective weights.
- Some errors in reference list.
- L225-226: not clear. Just because more processes and more parameters are included in a calibration, does by no means imply the calibration will be ‘better’ in some sense.
- Check for consistency in referring to (already) ‘frozen’ state vs. a (in progress) ‘freezing’ state.
- See attached marked copy for comments and corrections.
Status: closed
-
RC1: 'Comment on egusphere-2023-3122', Anonymous Referee #1, 01 Mar 2024
The presented manuscript presents a substantial volume of work performed however several major aspects of the presented study significantly reduce its quality and value.
1. Though the manuscript states a goal of establishing surface process complexity -- the cases that are supposed to represent different levels of said complexity are unrealistic and unjustified. No contemporary hydrological/coupled heat and moisture transfer model is forced with only Dirichlet conditions for surface temperature. This forcing can be imagined for models where no moisture transport is present (f.e. GIPL, some versions of CryGrid), however, these models are calibrated using a cost function that solely depends on soil temperature. Case 2 in that sense is even more odd since snow is universally represented in any model that is concerned with heat and water balance.
2. The spinup procedure in the presented study differs from commonly used ones (e.g. Evans and Ge, 2017; Lamontagne-Halle et al., 2018; Debolskiy et al., 2021). For scenario 0, it is unclear what the temperature or energy flux boundary condition at the top of the domain is set to (L135 only states "initial temperature"). The "freezing from the bottom" approach is unrealistic since in situ soil freezes only from the top.
3. Calibration procedure: It is not quite clear why a single objective function is used in this study for optimization. PEST software tool pwtadj1 calculates weights for observational groups based on contributions of the observational groups to the objective function and its derivatives. This approach is not particularly useful in the case of temperature and volumetric water content since these variables have different parameter sensitivity rankings. Moreover, Case 1 (for which, unfortunately, no mass top boundary conditions are presented in the manuscript) should not be calibrated with a cost function containing soil moisture. The model will try to compensate for the inadequate boundary conditions with calibrated parameters which is f.e. evident in the residuals histograms and figure 7. Instead, it would be more beneficial to run a multi-objective optimization algorithm (PEST software should have this capability), maybe with a metaheuristic such as Particle Swarm optimization, Differential Evolution (f.e. NSGA-II), etc. I would encourage the authors to compare the results between the calibration done with MOO and their results in the manuscript.
3.1 The authors do not consider the uncertainty in the observations to which the model is calibrated to. F.e. "volumetric water content" (which I assume is volumetric liquid water content) measured by DTS and FDR sensors under sub-freezing temperatures is subject to higher uncertainty than under positive temperatures thus former observations have to contribute less to the cost-function value.
3.2. Reduction of the parameter set for calibration. It is not quite clear how 21 parameters have been reduced from case 1 calibration to case 2 and case 3 calibration when in Table 4 all three cases have differences in calibrated parameter values in 18 out of 21 parameters. Moreover, in Table A1 only 9 parameters have bounds values for cases 2 and 3. Further comparing Tables 4 and A1 it is clear that a lot of calibrated parameters for different cases have values at the bounds or close to them. This further indicates that the calibration procedure needs more careful consideration from the authors.
Minor remarks:
1. Table 1 needs a rework since it is really hard to understand. In text (L140), there are only scenarios I,II and III mentioned.
2. Figure 4, Even with the current opacity it's hard to see all three cases's residuals. Consider making them line graphs instead or separating them into 6 subplots.
3. Table 4 and Figure 5. One of them is redundant.
4. Figure 6. Plotting RMSE and mean bias with depth would be much more illustrative than NSE.
5. Whenever the temperature is being ploted - it's benefitial to have 0 degree line to visually separate thawing/freezing. Also, figures like Figure 7 would benefit from having monthly ticks on x axis with months labeled instead of number of days.
Citation: https://doi.org/10.5194/egusphere-2023-3122-RC1 -
RC2: 'Comment on egusphere-2023-3122', Anonymous Referee #2, 15 Mar 2024
The authors investigate in the article the capability of a model implemented with an existing code (Advanced Terrestrial Simulator) to reproduce date from the Quinghai-Tibet Plateau (QTP) with three different upper boundary conditions. After a short description of the model (with slightly more information in the appendix), the calculation of the initial condition with a spinup phase and of calibration and validation, they shortly introduce the location and topography of the experimental site and finally present the results of the calibration process where the quality is measured by the residual as well as the nash-sutcliffe efficency (NSE) coeffient. Finally they compare the simulated temperature and volumetric water content with averaged experimental values and present results for energy and water fluxes at the surface.The paper is well written and the language is adequate. However, I have some major issues with the paper:
- First of all, there is major information missing. I did not find anywhere in the paper, how much snow there is on the surface of the experimental site and for which period of time. While there are plots about precipitation and snow fall rate in the appendix, they are in the rather unhelpful unit of m/s instead of mm/day and there is no information about yearly rainfal or snow water equivalent (only mean annual precipitation). This is an essential question for assessing, what upper boundary condition is reasonable. Still, according to the data in figure A1 and the mean annual precipitation of 405 mm given in section 2.5 this is not a dessert spot. Therefore, I do not see, why the authors assume that their case 1 scenario with only a prescribed surface temperature and no water input at all should result in a reasonable result (it does not as the NSE in figure 6 shows).
- According to section 2.5 the slope in the up-slope region, for which the numerical model was developed, is about 20 degrees. Therefore in the nearly saturated conditions when the active layer is thawed (with a volumetric water content of close to 40 percent) significant lateral flow is to be expected. This can not be handled by a one-dimensional model and might also be a reason for the extremely poor NSE in the lower part of the profile.
- There is very little data available to determine the huge amount of parameters (12 to 21 of the model). The authors write that "the number of observations greatly surpasses the number of parameters", but this is not really true. Most of the year the moisture content is either close to zero or close to saturation. The only information is in the time during which the transition occurs. The temperature at lower depth is also strongly smoothed, so there is also much less information than the number of days suggests. This should be taken into account in the calibration as well as in the assessment of the quality of the agreement. One of the central questions the paper needs to answer would rather be: Can a physically based model be calibrated with so little information?
- According to line 473-484 of the appendix the authors assume that during melting the density of snow is constant. However, everybody who has ever been outside in snow knows that there is a settling process. As a consequence the density of fresh powder snow is much lower than the density of a snow crust. This wrong assumption might result in major errors in the upper boundary condition.
- In their final simulations the authors compare the simulation results to experimental values averaged over several yearly cycles. However, the laws of physics refer to actual properties. As the processes in permafrost are highly non-linear, the averaged values will most certainly not be described by the same physical laws. Thus the comparison is meaningless.
- I find the histogram plots of residuals not helpful at all. They give no insight, where or when discrepancies are large or small. This would be necessary information, because it is relevant, if the model only matches the easy to catch phase during winter well, when everything is frozen or if it also is a good representation of the dynamic time during freeze and thaw. Besides, the box plot makes a comparison of the scenarios impossible. Points or lines would have been much better.
- Finally, the results obtained in the paper provide very little new insight into permafrost dynamics in general or in permafrost on the QTP in particular. Basically, an extremly simplified model (only temperature) gives very poor results. More realistic models are better, but with as little data, they still give poor results.
Although the paper is well written, I propose to reject it based on the stated problems of the approach taken and because of the lack of new scientific insight.Citation: https://doi.org/10.5194/egusphere-2023-3122-RC2 -
RC3: 'Comment on egusphere-2023-3122', Anonymous Referee #3, 24 Mar 2024
This paper applies the numerical ATS code coupled with the PEST calibration tool to compare different levels of complexity for representing the top boundary condition of a 1D freeze/thaw system.
Three cases are compared: a fixed surface T, and heat balance conditions with and without snow cover.
The paper is well written but needs clarifying and correcting; see comment below and in attached copy. Figures are clear and well-prepared. References are good. The methodology is justified.
The comparison confirms some previous published results including high sensitivity to near-surface parameters. Some other interesting explanations for sensitivities are also provided.
It is not clear how or if parameter interdependence (correlation) was accounted for. This could be an issue with so many parameters used for calibration.
There are issues in comparing these different scenarios.
I didn’t see any estimates of uncertainty or error in the input data used for calibration.
In Case 1, the proximity of the Dirichlet BC to the observed data seems an issue.
Specific comments:
- ‘mineral’ is used throughout the text to describe the subsurface layer below the peat. This is confusing especially when referring to parameters, as its not always clear if the authors mean the solid (mineral) phase or the bulk porous medium. Needs clarifying. Should be replaced with ex.: ‘soil’ or ‘sediments’. Check for clarity in parameters for this layer – if they assume dry or saturated conditions.
- L40: These are only the processes included here, they are not all processes as implied in the sentence. Similarly, L42: these are not the ‘main’ processes’, what about flow ? Needs rewording.
- L50: ‘to prevent cold air temperatures from reaching the subsurface’ needs rewriting. Yes, this is the net visible result, but of course heat can only flow from hot to cold so the process is the opposite: should say something more like ‘it prevents heat in the subsurface from escaping’.
- L54: ‘The degree of surface process complexity is determined by the climatic conditions in the study area.’… needs rewriting. The degree of simplicity/complexity depends on the applied modelling approach.
- L57-58 seems inconsistent. In one sentence conduction is said to (always) be dominant, in the next groundwater inflow is mentioned as being important.
- Fig 4: Case 1 residuals are not visible, I assume they are hidden behind the others ? Should bring them to front.
- Table 4 & 5… 5-6 digits is excessive precision. 3 digits is plenty.
- Eq 1: I couldn’t find the actual values of the objective weights.
- Some errors in reference list.
- L225-226: not clear. Just because more processes and more parameters are included in a calibration, does by no means imply the calibration will be ‘better’ in some sense.
- Check for consistency in referring to (already) ‘frozen’ state vs. a (in progress) ‘freezing’ state.
- See attached marked copy for comments and corrections.
Model code and software
Datamshapratirupa Radhakrishna Bangalore Lakshmiprasad https://doi.org/10.5281/zenodo.8273589
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