Initial submission: The manuscript "Potential impact of climate change on suspended sediment yield in NW Spain: A case study on the Corbeira catchment" by Rodríguez-Blanco et al. analyses projected climatic changes and their implications for sediment yield (SY) in a 16-km²-catchment in NW-Spain. The analysis builds on realizations generated within an ensemble of the A1B-emission scenario changing temperature, rainfall and CO2 concentration. The respective climate series are then used as imput with the SWAT model and the changes in SY compared. The study covers a generally relevant topic, even if it does not seem to play an important role in the selected study area with its relatively low SYs. The presented analysis is a logical complementation to the study of Arias et al. 2014. However, since it just looks at sediment output instead of water, it would arguably have been better to publish it in the same article. The manuscript is well and concisely written; the figures are of generally good quality.

Unfortunately, several issues have raised my concern. As the underlying model setup is the same as in Arias et al. 2014, they partially also apply there, though already published:

1. Blind faith in the models: None of the potential limitations of the model are considered nor even discussed. The most important points affect the applicability of SWAT to the chosen scale and degree of process representation.
2. SWAT being designed for medium to large catchments, is not a physilogical model for plant growth. While it may include an option for considering CO2, we cannot expect SWAT to ultimately simulate biomass dynamics requiring detailed knowledge on species-specific plant parameters, limitations by nutrients, temperature, water, etc. at the scale of HRUs.
3. Muskingum routing is not possible on daily scale at this area for numerical reasons. Especially considering the authors' statements of poor sediment connectivity (l. 117), it remains questionable if SWAT is the right model for these conditions.

4. SWAT using Curve Number approach to compute runoff "is not sensitive to rainfall intensity, so given a same amount of rainfall, SWAT computes the same amount of runoff regardless of intensity and duration of rainfall" (Arias et al. 2014). This is clearly a severe limitation for assessing erosion, which is very sensitive to rainfall intensities.

5. Disregard of potentially equally or more important aspects: The impact of climate change is manifold with multiple complex interactions. Naturally, a study usually needs to be limited to selected aspects. However, in the current case a clear justification for the chosen aspects (or the neglect of others) is missing. Thus, looking at T, P and CO2 the authors should first develop hypotheses what possible implications changes in these drivers could have according to the current state of knowledge. Then, it needs to be made clear and justified, which aspects can, and which cannot (or are not) considered in this study. Among the latter are paramount aspects like

6. landuse changes (It seems quite peculiar to assess the effect of CO2 on plant physiological response, but at the same time assuming constant land use and completely disregarding natural or anthropogenic changes in land cover. Other studies have shown that the effect of landuse changes can by far outweight any climate/hydrological changes. This should and can reasonably be covered with respective land use scenarios to compare their effect to the impact of the other factors.)
7. agricultural management (assumed invariant and only for a single crop, Arias et al 2014: It is quite strange to assume plants will grow differently, but agriculture will just stay the same)

8. changes in rainfall intensities and rainfall statistics (in this study prescribed in a very arbitrary way. Likewise, assuming unchanged wind speed, solar radiation, dew point, rel. humidity, but suggesting that CO2 will be the most important driver affecting transpiration seems somewhat unjustified.)

9. Generation of climate scenarios: The described generation of scenarios suffers from multiple shortcomings and ambiguous descriptions. The realizations of time series from a close-by station generated by regional models of the ENSEMBLES project seems to be a good starting point. However, the following aggregation across realisations (i.e. scenario mean) and across time (aggregating to monthly values) strongly reduces variability, which can have tremendous influence on sediment dynamics during extreme events. Instead, the realizations should be used as such as input for the model, and the respective model output analyzed for its variability. Likewise, I do not understand why the timeseries regionalized for the local station are not used directly. By using them with WXGEN, they are necessary altered, especially due to the fact that underlying statistics are used from the current observations only, thus assuming invariant variability in future.

Additionally to these major points, the manuscript contains multiple non-backed up statements, multiple minor inaccuracies, incomplete or ambigious descriptions of methods and referencing of apparently missing figures (see annotated PDF). I found the discussion hard to follow and partially drawing on findings or analyses not shown (e.g. seasonality, biomass, T-tests). There is no critical discussion on limitations of the approach whatsoever.

While points 2 and 3 might be remedied, unfortunately I don't see this for point 1. Anyway, a study thouroughly revised in that regard is effectively a comletely new work, therefore I'd rather recommend the rejection of the manuscript and with an invitation for resubmission.

Revised manuscript: The revised manuscript "Potential impact of climate change on suspended sediment yield in NW Spain: A case study on the Corbeira catchment" by Rodríguez-Blanco contains multiple changes which are explained in their response letter. I solely focussed on evaluating the responses to the issues I have raised in the first assessment (ignoring the issues raised by the other two reviewers). I found the authors have made efforts to remedy most of the minor issues raised. However, I could not detect any changes in the design of the actual study. This means the presentation changed, the story did not, which, admittedly, would have been difficult within this short time span. As such, my main three points of criticizm still apply. Moreover, I found the authors' response to them somewhat sloppy and generally unsatisfactorily (see commmented reply letter). Especially I found the vague formulations like "it is very common to find literature (papers published in high quality journals)" (without neither concret references) or "Some limitations of the model was included" (without any indications where the claimed changes can be found) very disappointing. In the discussion, there is no critical discussion on model-related limitations of the approach whatsoever. Thus, I cannot see a reason to revoke my assessement given in the first iteration: A study thouroughly revised in the necessary aspects is effectively a new piece of work, therefore I recommend the rejection of the manuscript with an invitation for resubmission.