The two reviewers agree the paper is a good contribution to the field of uncertainty evaluation of water quality models, the paper is on the whole well presented and I agree is fit for publication into HESS. The reviewers have clearly taken some time to read the paper thoroughly and their expertise on this matter is appreciated and equally where necessary the authors have responded well. I can see they will address all the points made by the reviewers in a satisfactory manner. However I have a few additional comments to make on the paper that I think need to be improved as well as the reviewer comments, these are generally minor but I think will improve the paper. However one is major and I think critical to address and was surprised this was not brought up in the review process (or I have miss-understood what has happened in the paper):

My major comments are on the expressions of the uncertainty limits which are for this paper very large in both cases (flow and SRP). The question I put to the authors is how these errors can be justified (no comment is made to the extent of these in the paper and it is absolutely critical to the whole model evaluation conclusions drawn). First the authors have chosen a parametric regression approach to the uncertainties in discharge – so the first point is are the assumptions in this approach valid (perhaps they could relate to Coxon et al. 2015) which used a non-parametric approach. 39% errors need to be justified I believe.
Secondly and more critically what the authors have done to calculate an ‘observational uncertainty’ value for the storm event behaviour is to use effectively a model error approach to their found discharge-concentration relationship (and perhaps pulled together from multiple events but not 100% clear and could do with some figures to better identify their approach). That is not daily observational error representation from the data they have. That is the error associated with using a simple expected relationship between discharge and concentration that will inevitably lead to much wider uncertainty limits than would be expected for a daily mean flow uncertainty value in my view. Furthermore they do not show how much this function is being used to extrapolate these errors elsewhere and if that can be justified to how these were lumped or otherwise in the first place.
Surely a much more sensible approach to trying to characterise the mean error of SRP for a day when they have event information is to first derive the expected uncertainty in the measurements themselves (which the authors have) and then resample these for these events to gain the actual observational uncertainty mean daily limits. Then they would be able ‘in extrapolation’ to take the discharge-concentration mean value and apply such limits to these. I would argue where there is data available to assess the actual mean daily uncertainty from high resolution samples then an appropriate method would show the range of uncertainty would be very different to those generated by the authors in this manuscript. I suggest this must be better evaluated before the paper is fit for publication. I further add their is no discussion of the chosen approach and any implications nor any comment as to how high the ranges of error are for the LoA compared to the general range of concentrations in the time series.

My other minor points include:
1) The intro states ‘In this paper we strive to identify and quantify the different sources of uncertainty in the data when the required quality check tests have been performed’ – yes but it should be made clear there are only some of the observational uncertainties that are dealt with here, and indeed maybe not some of the main uncertainties….
2) Whilst one approach to understanding observational uncertainties in water quality data is to compare when samples are taken this is not a full characterisation of the potential errors.
3) The comments on page 8 about comparisons to TOPMODEL are to me confusing. It makes it sound like TOPMODEL did some form of explicit routing between ‘grouped’ hydrologically similar points, but it did not, and this is only available in Dynamic TOPMODEL (Beven and Freer, 2001).
4) It makes no sense to me why this whole simulation is being run at 20m resolution. What is the point of this in terms of the landscape controls that need to be captured and the importance of such local parameterisation and interaction between cells that is either possible or critical. I do not see any justification in the spatial data presented nor the simple hypotheses presented about SRP that such fine detail is required. I feel the authors need to justify this far better in the paper (given they end up with only 2 drainage classes!)
5) Justify better how so many parameters can be really fixed and made homogeneous over the model domain please. No comments are made on this except the values are related to literature (does that mean they are all deterministic and not expected to vary in space?)
6) 15,000 simulations for 12 parameters is actually quite a small set. Please can the authors make comments about the acceptability of this sampling design given the needs of GLUE to sample the space effectively and how they confirmed this provided an acceptable simulation set.
7) On page 13 the authors state ‘model runs must fall within the acceptability limits’ – that would ONLY be the case if all errors in observations had been taken into account, but here as the authors make clear they are not including all sources of uncertainties so there is no need for this to be the case in their study.

So given I have made perhaps the biggest critique of the paper on a point that I believe is fundamental to what has been evaluated I have put back the assessment to an editorial review for the improved manuscript, thanks, Jim Freer

Comments from the editor

Thanks for your response to the author’s reviews and my own. But in fact I am not really yet in agreement with some of the rather quick justifications you have made to the manuscript on the basis of points I have raised so I would like these clarifying further please before I accept this for publication. These issues are important because if under the ‘limits of acceptability’ the methods are not clear how limits are quantified then in some sense they have no value as part of a considered experimental design.
1) The authors haven’t really justified either the use of using ‘prediction intervals’, nor that the error assumptions justify the parameteric approach chosen, on the basis of the observed information they have for the rating curve definition. I feel the authors need to deal with these matters better than they have done at the moment in formulation of GLUE LoA or discussion. Furthermore there is no clear rationale as to why a non-linear transformation in rainfall errors (not analysed) would in fact be a surrogate for using this parametric approach having wide uncertainties on the output as some kind of counter balance. I do not think that is well considered as written nor does it deal with the potential differences that might occur if the rainfall errors were . The same goes again for the discharge-concentration uncertainty. What is the proof the parameteric ‘prediction interval’ error model used relates to the observed error characteristics? – these are both important to get right and/or discuss the limitations/assumptions in them being used!
2) I don’t understand in the authors response what ‘We disagree that the method suggested here is better than ours’ is referring to. For a start I am not sure I stated a method was ‘better’, and secondly it is not at all clear what the context of this response is. So I would like that clarifying please. Perhaps it relates to 1) above…… but then it talks about discharge-concentration curves.
3) I’m sorry but I am not going to let this issue go of how you derive your load concentration uncertainties and at least make it clearer to the reader what you are doing because at the moment it does not seem consistent or it is certainly not written in a way that makes this year. To be clear from what I can read, you have constructed ‘parametric prediction uncertainty limits’ from the rating curve information. But then you actually do not use these in any way (as far as I can tell) to construct the load uncertainty estimates. You introduce a new model (and a very simple one at that), applied to every storm with a manually applied lag and you gain some very wide uncertainty bounds. Now there are good reasons why in that case the uncertainties will be large, and particularly if that very simple model is not good at describing the dynamics of the discharge-concentration dynamics. If fact as prediction uncertainties it could be argued it is significantly increasing what the potential error limits are in the observations of load. I understand that you need a ‘model’ (although I can still see other ways of doing this) because you wish to extrapolate beyond where you have ISCO samples over days. But that does not mean that you should attempt to be clear exactly what is being done, if that simple model is fit for purpose, the potential issues of increasing load uncertainty estimates over reasonable values if the model is not a description of the system and where you have data if you resampled the expected SRP uncertainties and the discharge uncertainties you have already calculated then what does that look like for the periods you can do this, that finally be clear that you do not seem to be using the uncertainties you have found in discharge to in any way quantify the prediction limits for this simple discharge-concentration model but instead use standard statistical errors that are yet to be proven. To me this is currently not very clear and not necessarily consistent and it needs to be better explained and discussed……
4) Regarding my minor point 1) noted previously the introduction still states ‘In this paper we strive to identify and quantify the different sources of uncertainty in the data when the required quality check tests have been performed’. Again this needs to be clarified there what the limits of this is in the paper (so only discharge and the P data)
5) I do not see how the response to my minor point 5 on the application of homogeneous parameters across the domain has been answered in the response given.
6) I think it needs to be justified far better than the response to minor point 6) is somehow justified for such a sparse sample. I’m not going to accept as a scientific evaluation that going from 15,000 – 20,000 simulations ‘looked similar’ without any justification of what that means. Nor that recognizes that one of the standpoints of using an approach such as GLUE is that the parameter space can be well sampled, or that if a sparse sample must be used there are experimental designs that improve the efficiency of sampling. In effect the authors have a parameter space they are trying to sample that even if they took 2 mid points on each axis this would require 2**30 simulations which is over 1 billion runs. So what convergence would be seen between 15-20K runs! Again the authors appear not to have recognized this at all and the response was not useful in my view and needs to be better justified if they are using GLUE.
7) Similar issues of not really providing a useful response go with the response to minor point 4) and 5). First there is still seemingly no analyses of why 20m DEM resolution is needed that is explicitly written in the model setup, so if somehow the hillslope characterization is being lost if the resolution was lower then in what way is some critical threshold being reached for the D8 sharing downslope? How has that been confirmed given the simplifications in general in the model? I still don’t see how this all squares with the authors own statement that the main SRP transportation processes are controlled hydrologically by valley bottom groundwater fluctuations (between page 6-7). Regarding minor point 5) here is nothing in the additional sentence added that at all discusses how these parameters are homogeneous across the catchment to the level they have been applied. No evidence is provided to say why that is realistic in the fully distributed model design or why 2 classes are the dominant hydrological-chemical classifications. This again needs to be improved and the responses were quite weak.

I have deliberated on these final responses for quite a while because although I appreciate the authors responses very few of the issues have been tackled head on in terms of changes to the core results or any further analyses. However I have always appreciated the additional comments and clarifications the authors have added to the manuscript. Given that on balance I did not wish the paper to be blocked by a set of points I brought up as editor vs the core reviewers and that I have talked this over with a few colleagues then I shall accept we have differences of opinion here and allow the paper to be published in HESS. I think this is the right approach to the review process and the extra work that the authors have done. The paper now has various additional points in it that better contextualise the way the results were generated and some of the rationale behind the experimental design and limitations of it so I am satisfied readers can develop their own view from this more clearly than they could before, Jim