the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
| 20 May 2026
Soil water forecasting for Australian dryland agriculture
Abstract. Soil water availability is a critical constraint to agricultural productivity. While soil water forecasting has previously been conducted in the literature for irrigated fields and surface soil (0–10 cm), there is a limited understanding of subsurface soil water in dryland paddocks, particularly in Australia. Due to rooting depth typically extending below 10 cm, subsurface soil water forecasts in cropping systems, for example, enable decision-making relating to sowing, fertiliser use, and seasonal yield potential. This study aimed to identify the best performing methods, and the underlying variables that affect accuracy when forecasting subsurface soil water (30–100 cm). The methods appraised in this study are Random Forest, XGBoost, Multi-Layer Perceptron (MLP), Long Short-Term Memory (LSTM), and an Encoder-decoder LSTM (ENCDEC). Various in situ and remotely sensed meteorological data were used to forecast soil water up to multiple months ahead, at 54 probe sites across Australia.
We find all models can perform with relatively similar accuracy for sub-monthly forecasts. For longer lead times, MLP and XGBoost performed better for sites with uniform rainfall throughout the year, and the memory-based models, LSTM and ENCDEC, better at sites with seasonally-dominant rainfall. Furthermore, we determine an upper limit to model utility, as accuracy can become poor many months ahead, and can be replaced by a historic average as an estimate. We find our models to be 'useful' up to 4 months ahead on average, after which accuracy is too low, or a historic average outperforms a model. We find rainfall intensity and seasonality, and model choice, to be key drivers of forecast accuracy at a new site. This study highlights the capability of elementary forms of each ensemble and deep learning model to provide sufficiently accurate soil water forecasts, particularly in the absence of a rainfall forecast feature.
- Preprint
(19427 KB) - Metadata XML
- BibTeX
- EndNote
Status: final response (author comments only)
-
RC1: 'Comment on egusphere-2026-2438', Anonymous Referee #1, 04 Aug 2026
-
AC1: 'Reply on RC1', Qazi Muqeet Amir, 09 Oct 2026
1. The model selection as outlined in the introduction is done more so on the basis of each model representing a different underlying mechanism, and the performance of each model, as it is in an elementary form, is able to highlight which mechanisms further models should base off of for future forecasting methods. The geographic imbalance can be addressed by merging the Summer and Winter zones into one 'Seasonal' rainfall zone, which can improve the 60-100 cm interval gap in our analysis. We can definitely add a paragraph to justify the exclusion of soil moisture products like SMAP and ERA5, that would be a great addition. They are excluded because the mass expansion and adoption of soil moisture probes in Australia over the past decade necessitate an understanding of their potential in forecasting without satellite data, and many soil moisture products, as detailed in literature, have a big training/validation bias towards the Northern Hemisphere. Also as at a grower level, the fine scale soil moisture predictions are needed, while most reanalysis or satellite products are very coarse. Hence the approach is centered on the potential to expand on the utility of existing probe-based infrastructure.
2. A more detailed explanation of the training design can be written out in the updated manuscript. The ENCDEC and LSTM do see sequential data (from past observation and past meterological forcing; Section 3.14 and 3.15).
3. The description of the deep learning training strategy can be written out clearer. Currently the hyperparameter tuning is optimised for the test set, which is leakage I agree, and we will rerun with the hyperparameter tuning only done on the validation period for the revised manuscript. The model training never sees the test data.
4. Conducted as a grid search with the same parameters as the LSTM (as both the encoder and decoder are LSTMs). Can be written out for the revised manuscript.5. The autoregressive properties are not being discarded as the LSTM and ENCDEC both see a sequence of the feature space, through which the LSTM unit learns the autoregressive relationship of each feature. Furthemore, to test the autoregressive nature of the forecasts, the ENCDEC decoder unrolls predictions with feed forward information (as a decoder LSTM is designed to do so). Hence the autoregressive nature of the feature and target are both studied in different ways among both methods, and were selected for this exact reason.
6) Code can be provided when the revised manuscript is submitted.
7) A wider parameter grid can be included, however the current extent of grids was carefully considered based on deep learning architecture that was successful in the literature and to account for mindful computation. However, a wider parameter grid will be considered for the revised manuscript that include max_features for RF and greater set of widths and depths for MLP. The XGBoost regularization has been considered, it is the parameter 'eta'.
8) All our runs are optimised for the same seed, and allowed with variable epochs depending on training patience to allow for convergence.
9) Can be rephrased in revised manuscript. But when we find that a certain model consistently performs well in a particular geoclimatic region or with particular meterological pattern, that can be used as a basis to choose that model at a new site if that new site has those same meteorological/geoclimatic properties.10) This will be better explained in the revised manuscript but since KGE' considers distance and timing in one metric, it was used for optimisation as to not favour one metric over the other. The correlation will be definitely added to understand timing for all parts of the analysis. The wetting/drying events will also be included in the revised manuscript.
11) To be added.Citation: https://doi.org/10.5194/egusphere-2026-2438-AC1 -
AC2: '[UPDATED] Reply on RC1', Qazi Muqeet Amir, 26 Oct 2026
Thank you to Reviewer 1 for taking the time to go through the manuscript in so much detail. We wanted to follow up on our earlier reply from 09 Oct 2026. The previous response was a bit prematurely posted, before the full author team was able to properly discuss the comments and it did not appropriately address the reviewer’s comments. It is also the corresponding author’s first time through the review process, and with consultation with the author team, a more considered response and comprehensive response has been provided. Please treat the responses below as superseding our earlier reply. We apologise for any confusion this may cause.
1) The methodological contribution appears limited. Benchmarking established models such as MLP and XGBoost, without introducing a novel architecture, theoretically grounded formulation, or substantive methodological advance, is insufficiently innovative for a 2026 study. In addition, the site-specific and geographically imbalanced dataset limits the generalizability of the findings and their broader contribution to data-driven soil-water forecasting. The authors should also justify the exclusion of meteorological forecasts and reanalysis products, such as ERA5 soil moisture. Incorporating these sources or systematically evaluating their added value could support more transferable models and provide a stronger benchmark for assessing the proposed approach.
In regard to your concern of the lack of innovation in method selection, our study is focused on determining which underlying mechanism is best suited for modelling soil moisture rather than proposing a model architecture. The literature currently contains many novel architectures built on different mechanisms, (e.g. tree-based or RNN-based, etc.), and each study tends to report their architecture as performing the best. Based on this trend, we believe any novel domain-specific architecture can be tuned to outperform alternatives within the domain for which it was developed. Hence, we compare the common underlying mechanisms directly, to identify which of them offers the best foundation for further domain-specific development. For example, future works forecasting soil moisture could use our results to decide (depending on their region of interest) whether to build on an encoder–decoder architecture or on a tabular structure such as MLP. By identifying the best-suited mechanism for each zone in Australia, our study informs future work on which mechanism to prioritise for a given region and task. Furthermore, the motivation of the paper is to enhance the use of soil moisture probes. Australia has many public and privately owned probe networks, but they are underutilised for forecasting due to a limited understanding of forecasting techniques. Hence, here we focused on using pure probe data to understand how they can be used to inform future soil moisture at the paddock scale. As written out in the introduction, the existing analysis of forecasting capabilities in Australia is either very narrow in spatial domain or is conducted for 0-5 cm remote sensed soil moisture. We believe, as also recognised by RC2, that there is a lot of novelty in our dataset being subsurface, dryland, and spread out across Australia. Even globally there is no study of soil moisture forecasting at this spatial and vertical scale (that is not all sourced from the same ISMN dataset currently employed across most soil moisture prediction/forecasting studies of this scale). In summary, the novelty is not only in the modelling approach but in the continental scope of the dataset, a focus on rainfed paddocks, and forecasting at depths beyond the soil surface.
Rainfall forecasts were excluded deliberately. Our aim was to assess how skilful soil moisture forecasts can be when they rely only on the autoregressive behaviour of soil moisture and on forcings available at the issue date, without any forecast information. This way the timing and magnitude of soil moisture peaks must be inferred from recent and historic soil moisture (both features in the model), rather than from explicit forecasts. We identify their inclusion as a direction for future work in the revised manuscript. We excluded gridded soil moisture products from reanalysis and remote sensing for a few reasons. Firstly, at a grower level, fine-scale soil moisture predictions are needed while most reanalysis or satellite products are very coarse. As mentioned earlier, our approach is centered on the existing probe-based infrastructure which invites the potential for improvement of paddock scale decision-making. We accept the coarse resolution for our meteorological inputs because weather is generally more homogeneous over such distances. We also did not consider satellite products as they estimate soil moisture only in the top 5 centimeters of the profile and we consider our feature space, particularly with in situ rainfall and soil moisture observations, at the issue date already capture the relevant surface conditions. Finally, many of these products carry systematic biases from the in situ data used to calibrate and validate them. This is a particular concern in Australia, where validation data are limited and spatially clustered, so we did not prioritise their inclusion. We will include a more explicit statement of why these have been excluded, with citations, in the revised manuscript.
2) The methodology is not clear. The authors should define one training example explicitly: forecast issue date `t`, target date `t+h`, every feature timestamp available at `t`, sequence/lookback window, target, and lead time `h`. This is essential because the paper calls the task forecasting but uses retrospective gridded and remotely sensed products. It is not clear what the forecast step is, what the issue date is, and what inputs are used. Does the LSTM use past observed or past series of meteorological forcing? If so, what is the lookback, and is this the case with other methods? If not, what is the usage of LSTM?
The ENCDEC and LSTM do see sequential data (from past observation and past meteorological forcing; Section 3.14 and 3.15). A more detailed explanation of the training design will be written in the revised manuscript and is outlined in response 3 below.
3) Validation, test use, and hyperparameter selection are ambiguous and may contaminate the test set. The text says tuning and training occur on a training set and the models are validated on a test set. Then it says high-performing combinations are "tested across all lead times" and selected for low KGE variance. What are the train, validation, and test sets? The final one- or two-year test period must remain untouched until all preprocessing, architecture choices, and hyperparameters are fixed.
The description of the deep learning training strategy can be written out clearer in the revised manuscript. Currently the hyperparameter tuning is optimised for the test set, which on reflection we agree is leakage, and we will reconduct the hyperparameter tuning on the validation period for the revised manuscript. The model training never sees the test data (outside the hyperparameter tuning, which will be corrected). We have an updated training/testing strategy for the revised manuscript described as:
“An independent model was developed for each site, depth interval, and lead time, for all models except ENCDEC. The ENDEC produced forecasts for all lead times from a single model per site and depth interval as it fed each subsequent forecast back through itself to make the next prediction. Each site’s record was divided chronologically into training, validation, and testing periods to preserve the temporal structure of the data. The final 365 days of valid observations (referred to as test year) at each site were reserved for testing, ensuring the same test year was used for every lead time and model at a site. The test period was not used at any stage of model training or hyperparameter tuning, and all performance metrics were calculated on the test period only. The remaining record was split chronologically, with the first 75% used for training and the final 25% preceding the test period used for validation. Training was stopped once the validation loss had not improved by more than 1% for 20 consecutive epochs, after a minimum of 20 epochs. For each modelling iteration the seed was set to be the same to ensure identical model initialisation across lead time, model choice, and depth interval. However, sensitivity to the choice of random seed was not assessed and some variation in performance between initialisations may exist.”4) How was the architecture of the encoder-decoder selected?
A grid search was conducted with the same parameters as the LSTM (as both the encoder and decoder are LSTMs). Please see line 232 and Table 1 as they outline the parameters tuned for the ENCDEC model in text.
5) If my guess is correct, for each lead time, a model has been developed. This point should be very clear in the text, but unfortunately, it is not. If this is the case, the autoregressive property is being discarded.
If the individual lead time point is unclear, we can ensure it is written out better in the revised manuscript. Please see response 3 for the updated details of the training and validation strategy. The autoregressive properties are not being discarded as the LSTM and ENCDEC both see a sequence of the feature space, through which the LSTM unit learns the autoregressive relationship of each feature. Furthermore, to test the autoregressive nature across the target domain, the ENCDEC decoder unrolls predictions with feed forward information (as a decoder LSTM is designed to do so). Hence, the potential to learn autoregressive nature of the feature space is tested in the LSTM and the potential to learn from the autoregressive nature of the feature space and the forecast domain is tested in the ENCDEC. The autoregressive nature of predictions is not discarded in either model, if anything is tested with incremental complexity across both methods.
6) Model implementations are not reproducible. Code and data should be provided. Based on EGU policies, this should have been flagged before archiving.
Code will be provided on resubmission.
7) Search spaces differ greatly in capacity and completeness. Random Forest does not tune `max_features` or depth; XGBoost does not tune the regularization parameters discussed at lines 181–183; MLP width is restricted to 5–12 units and its depth is undisclosed; the recurrent networks use small, different grids. Consequently, conclusions about algorithm classes may instead reflect unequal tuning budgets or constrained implementations.
A wider parameter grid can be included, however, the current extent of grids was carefully considered based on deep learning architecture that was successful in the literature and to account for mindful computation. A wider parameter grid will be considered for the revised manuscript that includes max_features for RF and greater set of widths and depths for MLP. The XGBoost regularization has been considered, it is the parameter 'eta'.
8) A fixed seed improves reproducibility but does not quantify variability. MLP/LSTM/ENCDEC results can vary with initialization and minibatch order. For fair comparison, an ensemble of seeds needs to be evaluated.
All our runs are optimised for the same seed but training is now based on variable epochs depending on training patience, each model should converge dynamically irrespective of seed. To account for mindful computation, rerunning every model to run for multiple seeds is impractical for us. However, this point is valid and has been reported as a limitation in the revised manuscript.
9) Models are trained separately at each site. Testing later dates at those same sites measures temporal evaluation, not evaluation at a new site. Zone summaries likewise do not constitute out-of-site validation. Therefore, please rephrase all "new site" claims or add leave-one-site-out/grouped-site validation in which the held-out site contributes no training, preprocessing, climatology, or tuning information.
We agree that this point can be stated more clearly, and we will revise it for the revised manuscript. The purpose of grouping sites by zone is to allow our findings to transfer to new sites. If a model type performs consistently well under particular meteorological conditions (accounted for in zones), it is a reasonable first choice at a new site that experiences similar conditions and provides practical value. When a grower installs a new probe, several years of data may be needed before a full model comparison is possible at that site. In the meantime, our results can guide the choice of model type for that location.
10) Hyperparameters are optimized using scaled KGE′, but models are ranked and interpreted primarily by RMSE. Explain why this objective/evaluation mismatch is appropriate and report both metrics on untouched test data. RMSE alone does not reveal bias, event timing, extremes, or uncertainty; add MAE, bias, correlation/KGE components, and performance during wetting/drying events.
This will be better explained in the revised manuscript but since KGE' considers distance and timing in one metric, it was used for optimisation as to not favour one metric over the other. The correlation will be added to the revised manuscript to understand timing for all elements of the analysis.
11) Without timeseries plots and more metrics, an evaluation cannot be completed.
We will add time series plots of observed verses modelled soil moisture and correlation as a performance metric to the revised manuscript.
12) The referencing needs an overhaul. For example, see the LSTM section. No reference for the properties is provided.
We can provide PyTorch and SKLearn reference for the method section to make explicity which modules have been used.
13) Many abbreviations are not defined or are defined late. e.g., ML, PCA, ConvLSTM, StemGNN, ....
Will be corrected in revised manuscript.
14) Many abbreviations have been defined several times. e.g., MLP, LSTM, RNN, ..
Will be corrected in revised manuscript.
Citation: https://doi.org/10.5194/egusphere-2026-2438-AC2
-
AC1: 'Reply on RC1', Qazi Muqeet Amir, 09 Oct 2026
-
RC2: 'Comment on egusphere-2026-2438', Anonymous Referee #2, 14 Sep 2026
The manuscript compares five machine learning methods (Random Forest, XGBoost, MLP, LSTM, and an encoder-decoder LSTM) for forecasting subsurface soil water content (30–100 cm) at 54 dryland sites across Australia, at lead times ranging from one week to 52 weeks. The authors classify sites into four "zones" based on rainfall seasonality and geography (Uniform, Winter, Summer, WA), evaluate model performance using RMSE and a scaled Kling-Gupta Efficiency (KGE's), define a practical "model utility" horizon (benchmarked against a historic climatological average), and use multiple linear regression to identify drivers of forecast error. The topic is relevant, and the dataset is a genuine strength; the paper fills a documented gap regarding subsurface, dryland, non-irrigated soil moisture forecasting. However, several methodological points need clarification before the results can be fully assessed, and the presentation would benefit from tighter quantitative support in several places. I recommend major revisions.
Major comments
Train/validation/test separation is insufficiently described (Sections 4.1, 4.3).
Hyperparameter tuning is performed via grid search to maximize KGE's at a 30-day lead time, then the selected combination is checked for generalizability across lead times, and finally models are evaluated on "the final 2 years of data." It is not clear whether this final 2-year window is disjoint from the data used during hyperparameter selection, or whether the same held-out period informs both. Please clarify explicitly whether tuning was performed with nested/rolling cross-validation on the training portion only, and state the exact boundaries of train, validation, and test splits.Unequal sample sizes across zones are not flagged where they materially affect conclusions.
Table 2 reports that 100% of Summer sites at 60–100 cm hit the RMSE benchmark, but the text later reveals this zone/depth combination consists of a single site ("the only available Summer site at 60-100"). Presenting this as a percentage in a table alongside proportions computed from many more sites (e.g., Uniform, n presumably >10) is misleading without a sample-size caveat. Please report n per zone/depth combination directly in Table 2, or add footnotes, and temper claims about the Summer zone accordingly throughout Section 5.3.1 and the Discussion.Explanatory power of the regression model (Section 5.4) is modest and underexplored.
The linear regression explains only 36–45% of RMSE variance. This is reported honestly, but given that soil moisture forecasting is known to involve non-linear interactions, it would strengthen the paper to either (a) test for interaction terms explicitly, or (b) briefly benchmark against a non-linear explanatory model to see whether substantially more variance can be explained, and to check whether the linear coefficients' signs and significance are stable.Zone definition logic is heterogeneous and should be justified more rigorously.
Three zones (Uniform, Winter, Summer) are defined by rainfall seasonality, while the fourth (WA) is defined by geography/soil texture independent of its (winter-dominated) rainfall pattern. The authors note that WA sites happen to all be winter-dominant, but this raises the question of why WA is not simply nested within "Winter." A short quantitative comparison (e.g., a table cross-tabulating clay: sand ratio and rainfall seasonality by zone) would make the rationale for treating WA as a separate axis more transparent and defensible, particularly since Section 5.4 partly attributes WA's anomalous 1-week regression coefficient to method-averaging artifacts rather than the zone definition itself.Attribution of RNN underperformance is speculative (Section 6, lines ~543–551).
The claim that LSTM/ENCDEC do not outperform non-sequential methods because of root-water interactions, irregular rainfall input, and depth is plausible but not directly tested in the current analysis. Since this is a central and somewhat counter-literature finding, it would be considerably strengthened by a targeted diagnostic rather than resting on narrative interpretation alone.Minor comments
- Eq. (1): The RMSE formula as rendered is missing the squared term in the numerator; "RSME" is also misspelled at line 280.
- Table 2 / Figure captions: Percentages in Table 2 should sum in a way that is checkable against Figures 4–5; consider adding raw counts alongside percentages.
- Figure 1 is referenced but never discussed in the text.
- Line 100: "this study focuses on understand forecasting capabilities" --> grammatical fix needed.
- Line 407: "forests" --> "forecasts."
- Reference list: The two Bureau of Meteorology "Meteorology, a" / "Meteorology, b" entries appear to be a bibliography-export artifact and should be corrected to proper author/organization citations.
Citation: https://doi.org/10.5194/egusphere-2026-2438-RC2 -
AC3: 'Reply on RC2', Qazi Muqeet Amir, 26 Oct 2026
We thank Reviewer 2 for reading the manuscript and providing critical feedback. Their comments have prompted revisions and we respond to each comment below.
Train/validation/test separation is insufficiently described (Sections 4.1, 4.3).
Hyperparameter tuning is performed via grid search to maximize KGE's at a 30-day lead time, then the selected combination is checked for generalizability across lead times, and finally models are evaluated on "the final 2 years of data." It is not clear whether this final 2-year window is disjointed from the data used during hyperparameter selection, or whether the same held-out period informs both. Please clarify explicitly whether tuning was performed with nested/rolling cross-validation on the training portion only, and state the exact boundaries of train, validation, and test splits.The train/test/validation split can be better defined in the revised manuscript. The hyperparameter tuning was over the test set, which is leakage we agree, and will be corrected in the revised manuscript. However, otherwise the model never saw the testing data. Here is the revises training strategy informed by reviewer comments:
“An independent model was developed for each site, depth interval, and lead time, for all models except ENCDEC. The ENDEC produced forecasts for all lead times from a single model per site and depth interval as it fed each subsequent forecast back through itself to make the next prediction. Each site’s record was divided chronologically into training, validation, and testing periods to preserve the temporal structure of the data. The final 365 days of valid observations (referred to as test year) at each site were reserved for testing, ensuring the same test year was used for every lead time and model at a site. The test period was not used at any stage of model training or hyperparameter tuning, and all reported performance metrics were calculated on the test period only. The remaining record was split chronologically, with the first 75% used for training and the final 25% preceding the test period used for validation. Training was stopped once the validation loss had not improved by more than 1% for 20 consecutive epochs, after a minimum of 20 epochs, and the model weights with the lowest validation loss were retained. For each modelling iteration the seed was set to be the same to ensure identical model initialisation across lead time, model choice, and depth interval. However, sensitivity to the choice of random seed was not assessed and some variation in performance between initialisations may exist.”
Unequal sample sizes across zones are not flagged where they materially affect conclusions. Table 2 reports that 100% of Summer sites at 60–100 cm hit the RMSE benchmark, but the text later reveals this zone/depth combination consists of a single site ("the only available Summer site at 60-100"). Presenting this as a percentage in a table alongside proportions computed from many more sites (e.g., Uniform, n presumably >10) is misleading without a sample-size caveat. Please report n per zone/depth combination directly in Table 2, or add footnotes, and temper claims about the Summer zone accordingly throughout Section 5.3.1 and the Discussion.
The unequal sample sizes will be addressed by merging the ‘Summer’ and ‘Winter’ and ‘WA’ zones into one zone, ‘Seasonal’. The seasonal dominated rainfall areas will likely lead to the same effect where the model must capture the timing of transition between wet and dry states and the soil’s response to longer periods of saturation or dryness, whereas the Uniform sites model the soil’s response to individual rainfall events occurring at any time of the year. This change and more detail on the split amongst zones will be added. Our revised manuscript will feature 24 Uniform sites and 27 Seasonal sites.
Explanatory power of the regression model (Section 5.4) is modest and underexplored.
The linear regression explains only 36–45% of RMSE variance. This is reported honestly, but given that soil moisture forecasting is known to involve non-linear interactions, it would strengthen the paper to either (a) test for interaction terms explicitly, or (b) briefly benchmark against a non-linear explanatory model to see whether substantially more variance can be explained, and to check whether the linear coefficients' signs and significance are stable.More advanced interactions have been conducted for the revised manuscript to improve on the R2 and test more complex non-linear interactions.
Zone definition logic is heterogeneous and should be justified more rigorously.
Three zones (Uniform, Winter, Summer) are defined by rainfall seasonality, while the fourth (WA) is defined by geography/soil texture independent of its (winter-dominated) rainfall pattern. The authors note that WA sites happen to all be winter-dominant, but this raises the question of why WA is not simply nested within "Winter." A short quantitative comparison (e.g., a table cross-tabulating clay: sand ratio and rainfall seasonality by zone) would make the rationale for treating WA as a separate axis more transparent and defensible, particularly since Section 5.4 partly attributes WA's anomalous 1-week regression coefficient to method-averaging artifacts rather than the zone definition itself.As detailed in an earlier response to your question, our revised manuscript features only two zones (as recommended by you and other reviewers), Uniform and Seasonal (merging WA, Winter, and Summer). There is a more rigorous justification for zone-based splitting of data in the revised manuscript.
Attribution of RNN underperformance is speculative (Section 6, lines ~543–551).
The claim that LSTM/ENCDEC do not outperform non-sequential methods because of root-water interactions, irregular rainfall input, and depth is plausible but not directly tested in the current analysis. Since this is a central and somewhat counter-literature finding, it would be considerably strengthened by a targeted diagnostic rather than resting on narrative interpretation alone.While a revised manuscript has not been requested, we have reconducted our results and analysis on all reviewer comments for our interest. The training/testing strategy and zone discretisation has been improved as recommended by all reviewers. The updated results show improved performance of the ENCDEC model, sufficient to change the conclusions from the current preprint. In the revised analysis, the LSTM and ENCDEC models perform the best, which aligns with the existing literature. We are grateful for the reviewer comments provided on this preprint discussion which have made the results and analysis clearer.
All minor comments are grammatical or formatting related and will be corrected in the revised manuscript.
Citation: https://doi.org/10.5194/egusphere-2026-2438-AC3
-
RC3: 'Comment on egusphere-2026-2438', Anonymous Referee #3, 29 Sep 2026
Soil water forecasting for Australian dryland agriculture
General comments:
- The introduction reflects that GRU architecture has shown the most promising results for soil moisture prediction, but it is not included in the tested models. Is there any particular reason for not including it?
- Mean annual rainfall is used to look at the forecast performance which is not really indicative of model accuracy for regions with seasonal rainfall.
- Site specific models will be fitted to site specific climatology and would have limited to no utility outside that specific site. It would be better to train the models with data from all the sites in each zone and compare with site specific results. Figure 6 suggests that no one model outperforms the other models when looking at the proportion of sites. Would it not be better to pool the ‘zonal’ performance via training using one model for all sites?
- Further details are needed about the model training data. What time periods are used for each variable? How is the spatial discrepancy between the site and 5km feature value dealt with?
- Nice figures!
Specific comments:
- Line 53: typo: MLPs consistently outperform conventional
- Line 59: Are MLPs or LSTMs the best performing? The paragraph above states MLPs but then in this paragraph it says LSTM.
- Line 70: Please rephrase the sentence: ‘They develop an architecture that pass their predictors and a LSTM encoded-decoded forecast of soil moisture at the preceding time steps to the target lead time into an LSTM.’
- Line 115: grammar mistake
- Line 140: Why is WA a different ‘zone’? How is different from ‘winter’ zone?
- Line149 : ‘The rainfall is calculated as the maximum between the in situ measured rainfall and the SILO modelled estimated rainfall at that site.’ How do you account for the spatial representativeness of the two different rainfall sources?
- Fig 4. Why is the RMSE shown as %VWC instead of the actual soil moisture values?
- Line 561: Rainfall is already used as an input. Is only historical rainfall used as input, not forecast rainfall?
Citation: https://doi.org/10.5194/egusphere-2026-2438-RC3 -
AC4: 'Reply on RC3', Qazi Muqeet Amir, 26 Oct 2026
Thank you Reviewer 3 for your insightful feedback, which has been addressed as follows:
The introduction reflects that GRU architecture has shown the most promising results for soil moisture prediction, but it is not included in the tested models. Is there any particular reason for not including it?
The GRU uses a similar recurrent neural network as the LSTM. Since both methods are sequential deep learning methods, the LSTM is used as representatively for sequential methods as testing every novel variety of a sequential model would be impractical. This can be written out more explicitly in the revised manuscript.
Mean annual rainfall is used to look at the forecast performance which is not really indicative of model accuracy for regions with seasonal rainfall.
We appreciate this concern and agree that mean annual rainfall on its own does not capture the seasonality, but it is not intended to. Mean annual rainfall represents the quantity of rainfall at a site where as the zone covariate represents rainfall timing as each zone receives rainfall in distinct parts of the year. Including both covariates allows the model to separate the effect of rainfall quantity from the effect of rainfall seasonality, rather than combining the two into one variable.
Site specific models will be fitted to site specific climatology and would have limited to no utility outside that specific site. It would be better to train the models with data from all the sites in each zone and compare with site specific results. Figure 6 suggests that no one model outperforms the other models when looking at the proportion of sites. Would it not be better to pool the ‘zonal’ performance via training using one model for all sites?
This methodology is valid given a grower would have access to multiple probes in a region. We are trying to add value to a single on field probe, as most Australian growers have. Particularly with the spatial scale of our agricultural regions, probes are often extremely spaced out and may not be very relevant to one another due to topographic, soil, and weather differences, so we are testing the relevance of the probe record at a single site. A pooled model would be on the basis of access to data from multiple nearby probes, which is not representative of our setting.
Further details are needed about the model training data. What time periods are used for each variable? How is the spatial discrepancy between the site and 5km feature value dealt with?
An updated paragraph will be dedicated to the training and testing design in the revised manuscript. The spatial discrepancy between the point reading from a probe and the 5 km grid size of weather features are assumed to be valid as we assume weather events are homogeneous over the span of a few kilometers, therefore the 5 km grid is an acceptable representation of conditions at the probe location. This is an assumption of course that we will report as a limitation in the updated manuscript.
Specific comments:
Line 53: typo: MLPs consistently outperform conventional
Will correct in revised manuscript.
Line 59: Are MLPs or LSTMs the best performing? The paragraph above states MLPs but then in this paragraph it says LSTM.
MLPs were stated to outperform conventional machine learning (non-deep learning methods) in Line 53. Line 59 states the superior performance of LSTM across conventional machine learning and deep learning methods.
Line 70: Please rephrase the sentence: ‘They develop an architecture that pass their predictors and a LSTM encoded-decoded forecast of soil moisture at the preceding time steps to the target lead time into an LSTM.’
Rephrased in revised manuscript.
Line 115: grammar mistake
Corrected in revised manuscript.
Line 140: Why is WA a different ‘zone’? How is different from ‘winter’ zone?
WA is distinctly sandier than any network which we can anticipate significantly impacts our expected soil-water behaviour at those sites. Line 138 explains this with citations. The updated manuscript however will have ‘WA’, ‘Summer’ and ‘Winter’ merged into one ‘Seasonal’ zone, so this issue is entirely overhauled.
Line149 : ‘The rainfall is calculated as the maximum between the in situ measured rainfall and the SILO modelled estimated rainfall at that site.’ How do you account for the spatial representativeness of the two different rainfall sources?
We do not downscale discrepancies on a spatial scale. That is a limitation to be reported as we assume rain events occurs over 5 km range (spatial resolution of the SILO dataset). Taking the daily maximum of the two sources was done to reduce the effect of missed or under-recorded events due to in situ apparatus malfunction.
Fig 4. Why is the RMSE shown as %VWC instead of the actual soil moisture values?
The %VWC is the volumetric soil moisture just reported as a % rather than a proportion.
Line 561: Rainfall is already used as an input. Is only historical rainfall used as input, not forecast rainfall?
We do not include forecasted features as our aim was to assess how skilful soil moisture forecasts can be when they rely only on the autoregressive behaviour of soil moisture and on features at the issue date. This way the timing and magnitude of soil moisture peaks are inferred from recent and historic soil moisture (both features in the model), rather than from explicit forecasted information. We identify the inclusion of a rainfall forecast as a direction for future work in the manuscript.
Citation: https://doi.org/10.5194/egusphere-2026-2438-AC4
Viewed
| HTML | XML | Total | BibTeX | EndNote | |
|---|---|---|---|---|---|
| 401 | 269 | 48 | 718 | 28 | 37 |
- HTML: 401
- PDF: 269
- XML: 48
- Total: 718
- BibTeX: 28
- EndNote: 37
Viewed (geographical distribution)
| Country | # | Views | % |
|---|
| Total: | 0 |
| HTML: | 0 |
| PDF: | 0 |
| XML: | 0 |
- 1
Amir et al. evaluate several ML models for soil moisture forecasting. Their results indicate that (a) DL models generally outperform ML methods such as MLP and XGBoost, and (b) how limited the models are compared to a "standard" threshold. While the application is relevant and the Australia-wide aggregation of probe records is potentially valuable, I do not see the manuscript as fit for publication. Several major concerns, in my opinion, should be addressed:
1) The methodological contribution appears limited. Benchmarking established models such as MLP and XGBoost, without introducing a novel architecture, theoretically grounded formulation, or substantive methodological advance, is insufficiently innovative for a 2026 study. In addition, the site-specific and geographically imbalanced dataset limits the generalizability of the findings and their broader contribution to data-driven soil-water forecasting. The authors should also justify the exclusion of meteorological forecasts and reanalysis products, such as ERA5 soil moisture. Incorporating these sources or systematically evaluating their added value could support more transferable models and provide a stronger benchmark for assessing the proposed approach.
2) The methodology is not clear. The authors should define one training example explicitly: forecast issue date `t`, target date `t+h`, every feature timestamp available at `t`, sequence/lookback window, target, and lead time `h`. This is essential because the paper calls the task forecasting but uses retrospective gridded and remotely sensed products. It is not clear what the forecast step is, what the issue date is, and what inputs are used. Does the LSTM use past observed or past series of meteorological forcing? If so, what is the lookback, and is this the case with other methods? If not, what is the usage of LSTM?
3) Validation, test use, and hyperparameter selection are ambiguous and may contaminate the test set. The text says tuning and training occur on a training set and the models are validated on a test set. Then it says high-performing combinations are "tested across all lead times" and selected for low KGE variance. What are the train, validation, and test sets? The final one- or two-year test period must remain untouched until all preprocessing, architecture choices, and hyperparameters are fixed.
4) How was the architecture of the encoder-decoder selected?
5) If my guess is correct, for each lead time, a model has been developed. This point should be very clear in the text, but unfortunately, it is not. If this is the case, the autoregressive property is being discarded.
6) Model implementations are not reproducible. Code and data should be provided. Based on EGU policies, this should have been flagged before archiving.
7) Search spaces differ greatly in capacity and completeness. Random Forest does not tune `max_features` or depth; XGBoost does not tune the regularization parameters discussed at lines 181–183; MLP width is restricted to 5–12 units and its depth is undisclosed; the recurrent networks use small, different grids. Consequently, conclusions about algorithm classes may instead reflect unequal tuning budgets or constrained implementations.
8) A fixed seed improves reproducibility but does not quantify variability. MLP/LSTM/ENCDEC results can vary with initialization and minibatch order. For fair comparison, an ensemble of seeds needs to be evaluated.
9) Models are trained separately at each site. Testing later dates at those same sites measures temporal evaluation, not evaluation at a new site. Zone summaries likewise do not constitute out-of-site validation. Therefore, please rephrase all "new site" claims or add leave-one-site-out/grouped-site validation in which the held-out site contributes no training, preprocessing, climatology, or tuning information.
10) Hyperparameters are optimized using scaled KGE′ but models are ranked and interpreted primarily by RMSE. Explain why this objective/evaluation mismatch is appropriate and report both metrics on untouched test data. RMSE alone does not reveal bias, event timing, extremes, or uncertainty; add MAE, bias, correlation/KGE components, and performance during wetting/drying events.
11) Without timeseries plots and more metrics, an evaluation cannot be completed.
12) The referencing needs an overhaul. For example, see the LSTM section. No reference for the properties is provided.
13) Many abbreviations are not defined or are defined late. e.g., ML, PCA, ConvLSTM, StemGNN, ....
14) Many abbreviations have been defined several times. e.g., MLP, LSTM, RNN, ...