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the Creative Commons Attribution 4.0 License.
| 30 Apr 2025
Model Predictive Control with Foreseeing Horizon Designed to Mitigate Extreme Events in Chaotic Dynamical Systems
Abstract. Practical applications of weather control are being explored under Japan's Moonshot Research and Development Program to mitigate extreme weather events such as heavy rainfall. One of the most significant challenges in this endeavor is identifying effective and efficient control inputs to mitigate extreme weather events within limited energy and computational time. To address this difficulty, the development of mathematical weather control approaches is being promoted. However, further improvements to the conventional approaches are required for the practical applications of weather control. In this study, we propose a novel framework called model predictive control with foreseeing horizon (MPCF), designed to mitigate extreme events in chaotic dynamical systems. The MPCF aims to improve control effectiveness by leveraging the sensitivity to initial conditions of chaotic dynamical systems. We evaluated the MPCF through control simulation experiments using the Lorenz 96 model. Our results demonstrated that introducing the foreseeing horizon improved the success rate without substantially increasing the computational cost of optimization, particularly when the control horizon was short. Furthermore, a comparison with the conventional method showed that the MPCF achieved success rates comparable to the conventional method with lower computational costs. This study showed that the MPCF is a promising control framework for mitigating extreme events in chaotic dynamical systems.
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RC1: 'Comment on egusphere-2025-1785', Anonymous Referee #1, 01 Jun 2025
This work addresses the mitigation of extreme climatic events through human interventions (e.g. cloud seeding to avoid torrential rainfall). The authors extend the classical model predictive control (MPC) framework with the introduction of a foreseeing horizon, which in a few words means that an extreme event can be foreseen with a longer horizon, and then prevented with an MPC optimization on a shorter "prediction" horizon in order to keep the computation time moderate. The capabilities of the proposed model predictive control with foreseeing horizon (MPCF) are extensively compared to those of MPC through experiments on the Lorenz-96 dynamical system.
As far as I can tell, the introduced method is quite original and promising. The presented experiments are convincing, showing a clear advantage over MPC and answering many (but not all) of the natural questions that arise from the presentation of the method. However, some statements made by the authors, although not crucial for their method, are at best misleading. Besides technical inaccuracies, there is still ample room for improving the general presentation of the paper.
I hereafter present a list of all the elements where I think that improvements can be made, ordered by their organisation in the paper rather than by their relative importances.
18 "Our results demonstrated that introducing the foreseeing horizon improved the [...] particularly when the control horizon is short"
-> at this point the foreseeing and control horizon are not defined, so a reader would have to guess what this is supposed to mean (especially the foreseeing, which is not classical).
I suggest briefly explaining what these horizons are (and that the foreseeing one is novel) before this sentence, in order to improve the overall clarity of the abstract.20 "a comparison with the conventional method showed that the MPCF achieved success rates comparable to the conventional method with lower computational costs"
-> the repetition of "the conventional method" is a bit inelegant65-85 Some arguments related to data assimilation are quite unclear.
First the authors say that "the EnKC, an approach based on a DA method, inherently calculates a control input only at the initial time of a DA window". This seems to suggest that all DA methods solve an optimization problem on the initial time only, which is false. Then, they say that "MPC is similar to variational DA methods in which the cost function is minimized within a certain time interval through iterative computations". Since variational DA is a subset of DA, this contradicts with the first statement. Besides, some variational DA methods (hard-constraint 4D-var) minimize a cost on the initial state only while some others (weak-constraint 4D-var) minimize a cost on the whole trajectory. Yet the authors do not make this distinction, and only refer to "4D-var", which is in fact more often used to refer to the hard-constraint variant.117 In equation (1), J_u and J_x are not explicited. Although the notations are quite intuitive, it would be preferable to include a brief explanation in the text, with some interpretation (e.g. J_x should be linked to the optimality criterion and J_u to the restrictiveness criterion).
128 On a similar note, figure 1 makes no reference to the cost function, so it is difficult to understand the purpose of the control.
The authors may consider making an "extrem value" appear like in figure 2 or simply modifying the legend of the figure.135 "MPCF introduces the new concept" -> MPCF introduces a new concept
150-168 The authors describe the content of figure 2 by introducing what looks like an algorithm, yet they do it with a rather informal description that lacks the clarity that would be expected from an algorithm. Typically, the fact that step 3 contains a condition like "if step 2 was skipped" is quite disturbing.
I recommand taking some time to think about potential improvements of this presentation.165 "The process proceeds" does not sound very good.
170 Figure 2: the subfigures a, b, c, d are not directly indicated on the figure. While it is obvious which is which, it makes the overall figure less readable.
181-183 it is really not necessary to introduce both variables n = 40 and k = n-1.
Classically only n (the number of model variables) is introduced, and I recommand the authors follow this convention.187 writing "5 days" instead of "5 d" would be clearer in my opinion.
189-190 the subscripts are inconstitent, I guess the authors wrote "u_k" where it should have been "u_i".
193 "Multiplying this value by dt is equivalent to the value of the control input in the case of direct addition to the state" is wrong in general. This statement only holds under the approximation of an infinitesimaly small dt, or when using the Euler integration scheme with a time step of dt, while the authors use the Runge-Kutta 4 scheme in this study.
203 Equation (4) -> have you considered using U_max = 0 (i.e. directly penalizing the squared norm of the control)?
You would certainly have to used a reduced penalty cost in this case. Perhaps a L1 norm would be a better choice too.
I would like to see some comments on these considerations. Some associated experiments would be greatly appreciated.207 "The scalar U_max \in R is the value that the norm of the control input is constrained to"
-> the formulation is rather misleading, as it seems to suggest that one wants the norm to stay close to U_max. Yet in principle a lower norm of the control would also be acceptable, although figure 3 seems to show that in practice the norm always remains close to U_max.
Besides, it is not even an inequality constraint, since in theory the norm of the control input could also go above U_max. The fact that this does not happen in practice is certainly due to a high value of w, which should be underlined in the text. Ideally, experiments analysing the influence of w would be a good addition to the manuscript.265 The indications of the tested values of T_p are contradictary between the first paragraph of section 4.2 and the corresponding row of table 2.
324 For figure 5, I believe that the sets of hyperparameters used to produce the points are not clearly described, outside of the fixed value of T_c.
For instance, why are there 3 points for MPC and 12 points for MPCF?
If only one hyperparameter varies, then it might be interesting to use the color of points to give this hyperparameter information,
and to differentiate between MPC and MPCF with the shape of the scatterpoints instead.Citation: https://doi.org/10.5194/egusphere-2025-1785-RC1 -
RC2: 'Comment on egusphere-2025-1785', Anonymous Referee #2, 05 Jun 2025
In this paper, the authors applied model predictive control (MPC) to Lorenz96. They proposed triggering MPC based on long-term and large ensemble model prediction which detects the emergence of extreme values. Their “foreseeing horizon” method improves the efficiency of MPC, which has a potential to contribute to mathematical optimization of weather control.
General comments:
Although the paper is within the scope of NPG, I believe this paper does not have a publishable quality. The issues raised below may not be addressed in a short period of time. Therefore, I recommend rejecting this paper.
First, the proposed method is not novel enough to be published in my opinion. Although the authors did not mention it, what the authors proposed can be recognized as event-triggered MPC in which the control process is applied only when a prescribed condition is met. The designed trigger of this paper is the predicted extreme variables above the prescribed threshold, and these extreme variables are detected by large ensemble prediction whose horizon is longer than the prediction horizon that the subsequent MPC process used. Generally, it requires a priori knowledge of the problem to design event-triggered policy. So, it looks to me that the authors proposed the original event-triggered policy suitable for controlling the Lorenz96 model, which is not a real-world problem. The authors guess that the similar approach is effective to weather modification, but it is a speculation and has not been verified. The paper provides neither generally applicable mathematical methods nor heuristic solutions to real geoscientific problems.
Second, the experiment design is flawed. The authors performed an experiment “14d before the time of the target extreme event”, so that in their experiment, the method “knows” that the extreme events will happen. In all experiments, it is necessary to perform MPC, and the authors do not need to worry about false alarms of their ensemble prediction in foreseeable horizons. This is unfair. Considering that the prediction gets rapidly worsened in the longer lead time, the authors’ foreseeing horizon may provide an adverse effect to mistakenly let controllers intervene the system for nothing. Also, I guess the authors quantified the computational efficiency of their proposed method based only on the cost of MPC optimization processes, and they did not include the computational cost for prediction in foreseeable horizons. If so, it is unfair. Their large ensemble extended forecast in foreseeable horizons is very costly especially in the weather modification context, although it can be run in parallel. I think that their primary claims of the advantage of their proposed method have not been fully supported by the experiments in the current form of the paper.
Specific comments:
Major points:
L35-40: These three key characteristics should be met in any control problems. For instance, any control problems should provide a solution in real time. I believe that the authors would like to say something different.
L63-64: Here the authors mentioned that the difference-based approach does not have an optimization process. But what is the optimization process specifically? Also, I think the optimality (or accuracy) of the solution is important, and the existence of the optimization process is not important. The difference-based method may not perform optimization, e.g., iterative evaluation of a cost function, but if the solution is very good, I’m going to be satisfied with it. I believe the authors would like to say something different.
L117: I think it is better to explain more about Equation (1). J_u and J_x are not explicitly defined.
L196: 200-member ensemble forecast for the 40-dimensional Lorenz96 model is apparently infeasible when it is translated into the real-world atmospheric model. Since the authors mentioned the advanced rapidity of their methods, I believe that the authors may evaluate their method with a feasible ensemble size. Maybe the authors think that MPC may not be able to be applied to the conventional atmospheric model, and they prepared the methods for future advanced AI weather models which are computationally efficient. Even in this case, the authors may explicitly explain if the large ensemble is absolutely necessary or not.
L310-315: I think it is more beneficial that the authors indicate the number of iterations in the optimization loop of MPC in addition to computational time. If the number of iterations is found, readers easily infer the potential computational cost in the real-world applications.
Minor points:
L10 & L28: Personally, I do not like mentioning a specific funding project in the paper. I believe that the authors can easily connect their work to the broader academic context without mentioning the specific project which does not last longer than the academic time scale. I’m not asking the authors to follow the instructions, this is just my subjective opinion.
L267: I think it is better to separate “Results and discussion” into two sections (i.e., “Results” and “Discussion”). In most cases, in the discussion section, the authors discuss their work, comparing it with the other work, and mention their limitations. It is a bit difficult for me to find the “discussion” part of this “Results and discussion” section.
Citation: https://doi.org/10.5194/egusphere-2025-1785-RC2 - AC1: 'Comment on egusphere-2025-1785', Fumitoshi Kawasaki, 07 Aug 2025
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