The authors conducted a meta-analysis to evaluate the performance of machine learning (ML) algorithms in the estimation of evapotranspiration. I believe this topic is timely and of interest to the HESS community. The motivation of the study, method, and results are clearly outlined, and they reach clear conclusions. Overall, this manuscript is informative and well structured. However, I believe there are several minor aspects which can be improved. Therefore, I support its publication in HESS with minor revisions.

1) L34 “ET is the most important indicator of the water cycle”: ET is not an indicator. It is a water balance component. Also, it may be not the most important component. I suggest writing “ET is one of the most important components of the water cycle ~”

2) L51-53: add examples and references to support the argument.

3) L82: define NDVI, EVI and LAI.

4) L83: define GPP

5) L153-155: I agree with the authors' point, but RMSE is still an important measure of the model performance. I think there is a way to normalize the RMSE when the magnitude or standard deviation of water flux are available. If possible, I recommend analyzing RMSE as well.

6) L225-229 and Figure 5 and Figure7: I think the authors should discuss variables which decrease the performance of the ML models (NDVI etc.). To do this, the authors may need to refer to Figure 7. Therefore, I suggest reordering Figures (i.e., 7 ->6 and 6->7). Figure 7 implies performance decreases due to NDVI (and other variables) may be spurious. In order to overcome such limitations, I suggest performing additional analysis by grouping ML models which use Rn/Rs and Ta and then generating Figure 5.

7) Figure5: difficult to compare variables. I think visualization can be improved by grouping variables which improve performance or not.

8) L261-263: I cannot agree. Data-driven approach and process-based approach are complementary. This should be revised.

9) L336-338: As the authors briefly mentioned here, eddy covariance observations are subject to random, gap-filling, and systematic (energy balance closure) uncertainty. There are several ways to address this uncertainty. For example, some studies may use a gap-filled dataset but some studies may choose observation only. Also, the energy balance closure problem can be addressed differently (uncorrected, Bowen-ratio corrected, and use of energy balance residual). Depending on this choice, the performance of ML algorithms may vary significantly (particularly energy closure problem is important). Although the authors mentioned observational uncertainty as a limitation of this research in L336-338, I believe this brief mention is not enough. If you can extract this information from the literature, I suggest performing an additional analysis (e.g., performance comparison for energy balance corrected vs uncorrected). If it is indeed difficult to extract the information from the literature, this topic should be discussed more thoroughly at least.

In this study, Shi et al., presented a meta-analysis of the performance of machine learning (ML) algorithms in the estimation of evapotranspiration. While this manuscript is interesting and within the scope of HESS, I have a few major concerns.

Most importantly, while this is a meta-analysis, the authors were comparing results from different publications, in which different data sets and sites may have been used. That being said, some of the results are not directly comparable. For example, Zeng et al. 2020, may have selected a few sites that are much more difficult to predict; and can not be compared with the results presented in another publication. Also, some sites may use in-situ estimates of LAI and VIs, while others use LANDSAT or even MODIS LAI and VIs. In order to make their results publishable, they need to find a way to harmonize the data sets used in all studies. Or, they need to justify that they have an inclusion criteria when selecting all publications (instead of just stating we searched on Scopus). In addition, I am not sure whether the number of models they chose can well support their comparison of so many features.

Also, the authors have another paper looking at similar topics (even with some similar pictures and texts) in discussion on Biogeoscience. As an example, in this paper:

Line 114-117: And in machine learning, in general, modeling with unbalanced data (with significant differences in the distribution between the training validation sets) may result in lower model accuracy.

And in the BG paper:

Line 91-94: Modeling with unbalanced data (where the difference between the distribution of the training and validation sets is significant even if selected at random) may result in lower model accuracy.

The only differences between the two papers is that the BG paper focused on NEE, while this paper looked into ET. I am not sure whether it is acceptable to publish two somewhat similar papers in two different EGU journals.

At the same time, overall, the writing of the manuscript is good. But I do find it difficult to follow from time to time. For example, the authors used many abbreviations without defining them (EVI, GPP and NDVI), and some of them may not be very familiar with all the readers.

Minor comments:

Line 34: I suggest that the authors refrain from statements like this, precipitation and runoff are at least equally important;

Line 52: detailed?

Line 155: I still do not understand why RMSEs are not used.

L186: outperformed whom? I believe that similar issues can be found in other places of the manuscript.