Review

The manuscript by Grandjouan et al presents a comprehensive sampling campaign in a mixed land-use catchment in France, aimed at characterizing runoff sources and their contribution to streamflow. A key strength of the study is the use of advanced biogeochemical signatures that combine traditional tracers (major ions, silicon) with less conventional ones (amount of aromatic carbon deduced from the spectral slope parameter), which are rarely applied in hydrologic studies but prove effective here. By employing 15 tracers that are present in variable proportions in the sources, the authors differentiate 8 spatial runoff sources and investigate their mixing ratios in stream water.

I think this is an interesting study that offers a novel way to look at runoff generation processes in heterogeneous catchments and may inspire future research. The authors are also transparent about the study's limitations. What I think is currently missing to reach publication level is some broader implications. As it reads now, the paper may appear like a project’s report rather than a scientific paper. I recommend the authors to “fly higher” and strengthen the abstract, introduction and discussion by highlighting broader (though not speculative) scientific implications.

I include various detailed suggestions that the authors should feel free to follow or not. I look forward to a revised version of the manuscript.

Detailed comments

22: the abstract states that microbial indicators are “analyzed” in the study but I am not sure such indicators are ultimately used in the mixing model.

60-61: “To this day, this approach is often limited to a vertical decomposition of streamflow according to groundwater flow, subsurface flow and surface runoff”. The literature on runoff generation sources, especially in forested catchments, is vast and is not limited to the cases mentioned here. I invite the authors to expand the literature.

Section 2.2.1. I found this section generally difficult to follow, partly because the distinction between a source and the sampling point used to represent it is unclear. I suggest following a scheme where first the source is presented and then its sampling strategy is clarified. I also found table 4 much clearer than table 1 to understand the sources but I had to wait until Section 3.1 to see it. Perhaps it could be merged with Table 1 or anyway presented earlier?

Table 1: the code for the quick surface runoff is missing.

210: It is difficult to justify that field/forest runoff composition is the same as rainfall. This is particularly the case for DOC and elements originating from dry deposition. But perhaps this does not have a great impact on the results. Can the authors just clarify which results may be impacted?

2.3.2: The selection of variables is an interesting aspect of the paper. I would recommend clarifying why some elements were considered in the first place (i.e. how they may be helpful even if they have been later discarded). This would be very useful guidance for other people to do a similar analysis. A clear summary of the selected parameters is needed at the end of this section, perhaps moving here some material from section 3.2.

227-229: I recommend separating what a biogeochemical signature is and what a mixing model (which require a whole other set of assumptions) is. Also clarify that the tracer does not need to be conservative per se (otherwise no tracer would work), but rather its signature from source to mixture must not be altered. The mixSIAR paper has a clear presentation of the working assumptions behind the mixture model.

235-237 “are used in this investigation, but [removed] from the parameter list for this particular task”. Unclear what this means.

2.4: I think the evaluation of the results could be more effective if the authors formulated the “null-hypothesis” that the runoff contributions from the different sources are proportional to their spatial extent. Rejecting the null hypothesis would help a reader see the potential of the approach to discover something new. I also see strong potential for using this method to validate outputs from spatially distributed models, which could provide alternative null hypotheses for comparison.

3.3: I think the uncertainty in the results for hydrological events should be better acknowledged and I invite the authors to only focus on the stronger results that hold true despite the uncertainty. An example is that FOR-2 is the largest contribution to the second event, since it does not appear a statistically significant result. I strongly advise to always report uncertainty along with the mean contributions. Same comment for figure 8: the plots are nice but do not show the likely very large uncertainty. Finally: I see that the discharge at Mercier vs Ratier changes significantly across storms. Is this attributable to rainfall spatial variability or runoff generation sources?

Figure 9 is very nice but I find the difference between the color of storage at high and low flow confusing. Is a different color really needed? I’d also recommend changing the water level in the stream in the different event scenarios.

Unclear sentences

Language is generally fine, but some sentences are overly complex. Feel free to use more often the direct active form, for example “we did this” or “we assume that”, rather than the passive form. In English, differently from other languages like French, this is totally fine and not considered informal.

35: “can alter water pathways”: as it is written now, it seems you are saying that pollutants can alter the way in which water flows along a pathway

70-72: unclear if the data also comes from the same catchments or only the application

117: the “main combination of factors”. This sounds rather vague. Can you be more explicit and clarify what this first classification represents?

This an interesting study putting forward the value of rich sampling of geochemical parameters in streamflow to trace back the spatial source of streamflow in a small peri-urban catchment with heteregeneous land use, in various hydrometeorological conditions. Such a data-based approach is valuable and could undoubtedly contribute to methodological advances and policy-level demands linked to water quality and runoff management in (peri-)urban areas.

I think the study has potential for publication in HESS. However, I have some concerns about the way some parts of results and discussion is carried out, which sometimes makes it hard to follow what the authors are getting at, although the overall message seems very clear at other times. I therefore suggest a major revision.

General comments:

• In the methodology and first part of the results, I am not sure to grasp why the authors present the full set of parameters they have measured (52) and even describe their patterns in the typology of source (sect. 3.1), since a significant portion of them is discarded in the subsequent signature build up used for source identification. In my view it introduces some confusion and the unnecessarily lengthen the manuscript. I provide some suggestions in the specific comments.
• I have mixed feelings about the robustness the end member mixing analysis conducted here. The way Section 4.1 seems to cast serious doubts on the ability to distinguish sources, especially regarding sewer system, urban & road runoff, and surface runoff. I appreciate the transparency of the authors in pointing at the limits of their approach, but as it stands I am left wondering whether the results presented can then be interpreted into a perceptual model, as is done in Sect 4.2. I think it owes in great part to the somewhat concatenated aspect the writing sometimes takes in the Discussion, where (sometimes strong) statements/ideas and comparison with the literature are given in one sentence without really connecting with a conclusion. This concerns both Sect 4.1 and 4.2. Examples include:
  •  L480-481: where wastewater source is concluded to be indistinguishable from URB without much nuance or discussion of the implications
  • L495-501 where the robustness of using precipitation as a proxy for runoff signature is questioned, then a reference is used to say that it is sometimes valid, without stating whether the referenced study was done in a similar context, making the overall argument somewhat weak.
  • L530-536: where the authors start from describing a fill-and-spill (which was not only described in the Panola catchment, see Spence & Woo, 2003; McDonnell et al., 2021) to arguing that “quick surface runoff is favored in grasslands” (as compared to what?), based on a lower water demand than forest and crops (an assertion which is not always true, see for example Houspanossian et al., 2023), and then a last sentence about dry soils...connected to the previous statement? What is the conclusion then?
    
    
    
    I would thus suggest to rework the Discussion thoroughly, to improve fluidity and clarity.
• Also, Grandjouan et al. (2023) considered three subsurface sources in their analysis : colluvium aquifer, but also a fractured aquifer and saprolite, with significant, seasonally-variable contribution from all of them. I am guessing that the latter two (fractured and saprolite) being widespread over the catchment (as opposed to the colluvium), the more spatialized analysis proposed in this study implicitly includes a spatialization of fractured and saprolite contribution to streamflow embedded in FOR-1, FOR-2, AGR and GRA sources. Yet, it does not seem to me that this link between the sources identified in Grandjouan et al. (2023) and the present study is clearly made, although this previous is cited several times especially in Sect 4.2. This link should thus be more thoroughly put forward in the Discussion, to better show how this study builds up on Grandjouan et al. (2023) and the associated benefits.

Specific comments:

L139-140: can the authors justify the choice of 3mm-threshold to distinguish dry and wet periods? It seems quite a low threshold, and 3 mm in 5 days is not intuitively “wet” in my view.

L148- : Braud et al (2018) is missing from the reference list, so it’s hard to know what the original method was.

L150-151: Can the authors give more details on the configuration of HCA used here, e.g. how the optimal number of classes was found, was is done using absolute or relative concentrations, etc.

L156-157: please provide a reference and/or justfication for this API, notably the k=0.8 factor. As it stands, it seems somewhat arbitrary.

L157-158: I am not sure to understand the reason behind choosing two events per class, instead of 3, 4...please develop if there was a specific reason.

L223: is it hierarchical classification, or clustering?

L2333-238: since a part of parameters can be eliminated from the target signatures even before measuring them, just by their nature (non-additive, undefined relations with abiotic factor, too reactive), I do not see the point of initially listing them in the previous sections nor describe how their are measured, as they do not serve the current study. I would therefore recommend to move this reasoning earlier in the methods and remove the corresponding parameters’ (UV*, Fe, phosphates, etc.) protocol from the main text and even from Table 3. This may streamline the manuscript. The case is different for the parameters removed as per screeing test described in L238-244, as I understand that measurement was necessary before screening out these parameters.

Figure3: this is a figure with a lot of information. I would suggest to keep the parameters effectively used for later source identification (which are not even put put in the axis/caption at present), which would make it much more readable and easier to interpret the “relevant” patterns and clustering for the later analysis. Perhaps the “full” figure can go to the Supplementary materials.

Fig. 3 & 5: how were the concentrations standardized? It seems like an important point of methodology to interpret the results, all the more that the range are quite different between the two figures, hence the method?

Fig. 6 & 7: It may be interesting to add the corresponding figure with absolute flow amounts (perhaps in the Supplementary Materials) to put these results in perspective of m3, as is already done somewhere in Sect. 3.3.2 (e.g. for SEW contributions in m3 during events), but without graphics.

Fig. 7: Also, is it stated somewhere why 6 March 2019 and 22 June 2022 were not sampled at Ratier and Mercier, respectively ?

L389-391: an estimate of the rainfall amount leading to sewer overflow would be informative.

L409-411: This sentence seems more of a discussion point. I would suggest to move it to Sect. 4, possibly developing this interesting point, especially if local or comparable references on rainfall spatial variability and variable sources activation are available.

L412-414: Again, this seems like a Discussion item, but as it may already be somewhere else, I’d recommend to remove this sentence.

Fig. 8: this is a nice figure, combining important information. Yet, it is hard to tease out the relative contribution of sources since the “total” bars sometimes drastically change in height. I wonder if as companion, supplementary figure wouldn’t be useful to visualize the temporal changes described in Sect 3.3.3, with a 0-100% y-axis for stacked contributions. If technically possible, superimposing the discharge time series on a econd y-axis (same as now) would be nice.

L450-452: these absolute numbers are very informative, such comparison would have welcomed already in Sect 3.3.2 circa L401-402.

L456-461 : the statement are phrase in a very general way, this introductory paragraph may benefit from (subtle) reminder it applies to the current study: “In the studied catchments, …” or “In this study, …”

L481-485: this is an interesting point, it seems to me that this research group jointly analyzed stable isotopes and other chemical signatures in their end member analysis. At any events, I am not sure to understand what the authors are here concluding, please clarify.

Fig. 9: what is the yellow storage? Storage amplitude between dry and wet conditions?

L537-539: Having the same geological features does not necessarily result in having the same hydrological behavior ; topogaphy, land use (and thus water demand and timing). The next sentence seems in contradiction. I think this part needs some rephrasing.

L555-567: This reads as a summary rather than a conclusion ; this is more the function of the abstract, so I would suggest to significantly reduce or remove this part.

Technical comments

L394: from Fig. 7, I read a 32%-contribution of URB to the event on Oct ‘21 at Ratier, not 22% as in the text.

Figure 8: the color code is the same as Fig. 6-7, but not the legend order, it would help to homogeneize.

References

Houspanossian, J., et al., Agricultural expansion raises groundwater and increases flooding in the South American plains. Science380,1344-1348(2023).DOI:10.1126/science.add5462

McDonnell, J. J., Spence, C., Karran, D. J., van Meerveld, H. J., & Harman, C. J. (2021). Fill-and-spill: A process description of runoff generation at the scale of the beholder. Water Resources Research, 57, e2020WR027514. https://doi.org/10.1029/2020WR027514

Spence, C., & Woo, M.-K. (2003). Hydrology of subarctic Canadian shield: Soil-filled valleys. Journal of Hydrology, 279(1–4), 151–166. https://doi.org/10.1016/S0022-1694(03)00175-6