Dear authors,
thank you very much for your swift response to the reviewer comments. As you have seen, the two reviewers provide contrasting evaluations of your manuscript. After re-reading both, the manuscript and the reviewer comments, I think both reviewers point out aspects in your manuscript that are not fully clear. I do not fully share the critical assessment of reviewer #1, as it seems, in principle, a communication problem. However, the onus here is on you, the authors to unambiguously and comprehensively describe your experiment for it to be reproducible and to avoid misunderstandings. Even if a full description of the method and the associated assumptions may be provided in detail elsewhere, a concise description of the main points and assumptions/limitations may not only help the reader, but should be good practice in any scientific research paper.

Similarly, as remarked by reviewer #2, it would be of tremendous help if the science question addressed in the experiment was more explicitly stated together with a clear research hypothesis that is going to be tested. This is missing - lines 61-76, referred to in your response, are very vague and mix up earlier work, with a very short statement of what is done in this manuscript, without any clear statement of the problem and why it is important to address it and how you do it (i.e. the hypothesis to test).

Another point I would like to mention concerns your reply to reviewer #2:"The logic here is that if the observed changes to streamflow are driven by changes to meteorological forcings, then there should be no changes to the model parameters (assuming the prior parameterisation and model represent the catchment properties and processes well)."
I am not sure that the underlying assumption does not hold. The hydrological system is at the interface of atmosphere-pedosphere-ecosphere, which are linked through a vast system of interactions and feedbacks. If the meteorological forcing is changing, the other boundary conditions of the system are also changing (co-evolving) at a wide range of temporal and spatial scales. Just one example: change the meteorological pattern (e.g. rainfall seasonality or snow pack timing) and this will (potentially very rapidly) change the not only vegetation but the entire ecosystem and thus the partitioning between storage, drainage and evaporative fluxes and thereby the underlying model parameters (e.g. hydraulic connectivity or soil storage capacity).

I would be glad to receive a revised version with *detailed* clarifications and more explicit explanations of the research objective/science question (including research hypothesis) and the methods used including the associated assumptions, a justification for these assumptions and potential limitations of the method.

Best regards, Markus Hrachowitz

Dear authors,
the revised version of your manuscript was reviewed by one referee, who highly appreciates your work but who also raises some concerns that need to be addressed before the manuscript could be considered for publication.

As in the first round of reviews, also now the reviewer points out, and i tend to agree, that the motivation, scope and research questions are not described in a sufficiently clear and detailed way. In other words, what is the knowledge gap that this study attempts to close? What is the novelty of this study and how is it different to other studies. The reader would highly appreciate more clarity on these points.

The reviewer also points out that the study could strongly benefit from a more suitable choice of the benchmark or at least a discussion on the limitations of the chosen benchmark. Similarly, the discussion on several other points needs to be strengthened. The reviewer provides a range of interesting questions that can help to shape the discussion.

I am looking forward to receiving a revised version of your manuscript, addressing all the reviewer comments in a as detailed as possible way.

Best regards,

Markus Hrachowitz

Dear authors,

thank you very much for the revised version of your manuscript. I appreciate your efforts to clarify the remaining questions, which I feel you have done in an excellent way. I would just like to comment on your remark that a "benchmark" was not used and that this is also not necessary. In general I feel that when adding information (in its most general sense) to a model, as was done here through data assimilation and time-varying parameters, it is always quite informative to compare the new model outcome to one without this information (i.e. a benchmark), to actually quantitatively illustrate the effect. It is true that you do not use the actual term "benchmark" here. But as far as I understand Figure 6 and your statements in the abstract and on p.20 and 23, you actually and laudably compare the TVP results to results from a model run using time-invariant parameters, which in my understanding is a benchmark. I may have missed it, but it would be a nice bit of additional information if you could add (1) a short statement in the methods section explicitly explaining that you compare the time-invariant model output of the post 1979 period (which already is a split sample, as the model was calibrated pre-1979 only) to the time-variant model outputs for that period and if you provided (2) some sort of quantification of the improvement.
Apart from that I believe that this is a very interesting study, which I would be glad to accept for publication once these final adaptations are added.

Best regards,

Markus Hrachowitz