The manuscript proposed to use convolutional neural network (CNN) associated with gridded meteorological data for Karst spring discharge modeling. CNN was applied to three karst spring watersheds in Europe. Results of 2D CNN model associated with gridded meteorological cells were compared to that of 1D CNN using climate station input data. The manuscript is well written and technical sound.

General comments:

1. CNN is a mature data-driven tool which highly relies on data availability and quality. The authors argue that less data is needed in the proposed approach to obtain satisficing results compared to previous deep learning approach and overcome the short of data from climate stations. The results show that 2D modeling is not necessary better than that of 1D and previous modeling in Lez spring. A question raised is that whether the key input data has been identified. For example, pumping may play an important driving factor but is not included in training and screened out by Bayesian model. Gridded meteorological data may not be enough to improve the model performance. The authors needs to address their contribution. Guide line for data preparation will be helpful for the suggestion of use machine learning.
2. The modeling uncertainty is quite low to almost without uncertainty that seems abnormal. The authors may explain this.

Specific comments:

1. Line 203, write the long short term memory for abbreviation of
2. Lines 213-215. Although the all programs are available from Python community. Technical functions should be described for the used library or framework should be explained.
3. It is not clear functions for training, validation, optimization and testing periods in Table 1. The should be explained in main text.

This study uses convolutional neural networks (both 2D and 1D) to model streamflow in three karst spring catchments.  They compare 1D CNNs, which process time series of weather station forcing data, to sequential 2D – 1D CNNs, which process gridded meteorological forcing data from climate reanalysis.  The use of widely available gridded meteorological data is advantageous due to its more complete spatiotemporal availability, in comparison to data from weather stations.

This is an interesting study with potentially applicable results; however, there are several key limitations with its current form.  The literature review at present is insufficient and does not provide enough information to explain the relevance or context of the results.  In many cases, the likelihood of hypotheses and claims is stated without justification.  Additionally, conclusions surrounding the potential of these models for karst catchment localization and delineation are currently overstepping the results shown.

Major comments

Overall, the introduction is very brief and does not provide adequate context for the current work.  Johannet et al (1994) is referred to but it is not stated what they did.  The authors can expand to consider the further history of ANNs in water related research (e.g. Hsu et al 1995, Maier and Dancy 1996, Zealand et al 1999, Maier and Dandy 2000 and the references therein), which can lead to the use of deeper networks in water research.  Additionally, 1D CNNs have been used for streamflow prediction in the past by others who the authors do not refer to (e.g. Hussain et al 2020, Van et al 2020).  By further fleshing out the relevant history the authors can more convincingly present the relevance and potential applications of their work. 

Why do the authors use a 1D CNN to learn temporal features rather than an LSTM, despite the many successes of LSTM-based modelling for streamflow prediction (e.g. Kratzert et al. 2018, 2019a, 2019b; Gauch et al. 2021, Frame et al. 2021, Anderson and Radic 2021; note that this list is not comprehensive or that all required but these papers can be a starting point for the authors to consider)?  While there is a brief mention that 1D-CNNs are fast/stable, there is little mention or consideration given to the vast success of the LSTM approach at both daily and hourly scales, which is surprising given their prevalence.  This study uses only three catchments and so I can’t imagine that the training time between a 2D – 1D CNN model vs a CNN-LSTM model would be prohibitively different.  There is opportunity here to compare the two approaches quantitatively to see which performs better (e.g. perhaps a CNN-LSTM model will be able to simulate the streamflow peaks around Oct 2020 in Figure 3), or if there are differences in the “catchment delineation” results.  While the authors don’t absolutely need to perform this comparison, it would certainly help to justify their methodological choices (2D-1D CNN vs CNN-LSTM).  

In many cases, the authors assert the likelihood of a claim without justification.  These instances either need further exploration or to be reframed as “possible” rather than “probable”.  For example, in line 297 it is stated that the main source of uncertainty is “probably the uncertainty of parameter values resulting from the ERA5-land grid cell sizes”.  How are the authors confident that this is “probable”?  Are the authors referring to the uncertainty, or error?  There are other places where the authors describe a result or hypothesis as being “probable” without any justification.  These instances are more conjecture than a discussion of probability (e.g. line 344, line 359, line 363, among others) and are not very convincing without additional support.  Furthermore, there are instances where highly certain language is used without quantification (e.g. “perfectly” in line 297) or a contradictory mixture of language is used (e.g. “probably perfectly” in line 360; “quite exactly” in line 411).  These should be changed as well.  Another example is in line 407, where the authors suggest that the shape of the sensitivity pattern may be a “relic from spatial correlation of precipitation events”.  Can this hypothesis be supported or explored with evidence?  The authors have the needed precipitation data so I am not sure why this conjecture is here without support.

I have concerns that the sensitivity methods applied do not actually work to “delineate” or “identify” the catchments to the degree that the authors are claiming.  One key difference between Anderson and Radic (2021) and this study is that the basins in Anderson and Radic (2021) are in different regions of the input space, while the basins here are all centered (Figure 6).  Having stations in different regions of the input was key to interpret if the model was learning to focus on the right regions in Anderson and Radic (2021); e.g. in Figure 7 in Anderson and Radic (2021), the model is sensitive in different regions which tells us that the model is learning different things for different stations.  In Figures 6 and C1, one could argue that the models here have learned to generally focus on the central area under all circumstances and it is just coincidence that the basins are centered there as well.  As I see it, in order to make steps towards catchment delineation, the authors need to demonstrate that the model automatically focuses on (1) the right location and (2) have the right “area of sensitivity”.  Neither of these points are quantified in this work, while both are referred to qualitatively; however, both can (and should) be more rigorously investigated.  To point (1), the authors could run different tests with the basins placed at different locations in the input (e.g. 9 (or more) models could be made for each basin – one with the basin located in the top left area of the input, one with the basin located in the top center area of the input, etc).  Then, the location of maximum sensitivity can be quantified and compared to the location of the basin.  In this way (or in some similar way), the authors could more concretely conclude whether their approach is learning to focus on the correct area of the input or not.  To point (2), the authors could run different tests with different input areas (e.g. for each basin, the authors could double/triple/etc the number of pixels in the x- and y- directions).  Then, the “most sensitive area” can be quantified (e.g. the area greater than the half-maximum sensitivity, or some alternative metric) and compared with the basin area.  The authors can find: is the most sensitive area always comparable to the known basin area?  By addressing these two points (either as described above or in some other way), the authors can more convincingly state whether the CNN approach has potential for catchment delineation. 

Additional comments:

Paragraph starting at line 43: This paragraph can be hard to follow when very little has been done to describe the architectures (e.g. the acronym ‘LSTM’ has not been defined).

Line 55: The authors state ANNs to be superior for points i) and iii), but no justification is given as to why they expect this.

Line 200: Add references for batch normalization (e.g. Loffe et al, 2015) and dropout (e.g. Srivastava et al, 2014)

Line 203: LSTMs are claimed to be slower and with similar performance as compared to 1D CNNs for “this specific application”.  Does that mean that the authors have used LSTMs for streamflow modelling in karst catchments as well?

Section 3.2: It would be very useful to have an overview of the models that were used.  Currently in Table 1 there is the time splitting scheme.  In addition, it should be more clearly listed the length of the input sequence, number of observations, and number of parameters in each model (or layer).

Section 3.4:  This section is very brief and does provide much context for the methods chosen (e.g. why follow Anderson and Radic, and not other interpretability methods?).  Some statements are vague (e.g. “In short it works by perturbing spatial fractions of the input data by using a 2D-Gaussian curve” – what is meant by ‘using’?).  The final few sentences are written with certainty, although the methods have not been applied yet (e.g. “… a smaller area will most certainly have a higher influence on the spring discharge…”).  This section can be challenging to follow, and I suspect especially so for readers who are not as familiar with Anderson and Radic (2021).

Line 254: How is “satisfying fit” qualified?  Satisfying as compared to what?

Line 276: It is not surprising that the models are within the same “order of magnitude”.  An order of magnitude of NSE spans 0.1 through 1, which is a huge range of performance.

Sections 4.1 – 4.3: These sections are a mixture of results and discussion.  While that is not inherently an issue, both results and discussion are mixed throughout each section in ways that vary from section to section (e.g. 4.1 begins with results, but 4.2 begins with discussion before even a description of Figure 4).  It would be easier to read and follow if the authors were more consistent between sections (e.g. first have results of 4.1, then discussion of 4.1, then results of 4.2 etc). 

Line 331: It seems the authors mean “substantially” and not “significantly” as there is no discussion of statistical significance here.  “Significant” is also referred to in author places where the authors do not appear to mean it in the formal sense.

Line 339: If this new model is not going to be discussed or explored clearly, then it should not be brought up at all. 

Lines 371 – 377: This is description of other studies should be moved to the introduction.

Section 4.4 (and Section 3.4): It is not clear how the authors are defining catchment delineation/identification.  Are they referring to the areas of the sensitivity fields that are greater than the half-maximum of sensitivity?  For which input variable?  It should be clarified just how the step from sensitivity heat map to catchment delineation could be made.

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