Dear Dr. Chen et al.,

Thank you for submitting your work to Biogeosciences. Your manuscript has been evaluated by three reviewers who are all experts in this field. As reflected in the reviewer comments, there are a number of major concerns regarding the statistical and methodological details, structure and clarity of discussion, robustness of conclusion and many others that would need substantial improvements. The reviewers have provided a list of constructive comments and suggestions that are certainly of value to your revisions.

I consider this a Major revision. The fate of the manuscript would depend upon the quality of your revisions. Please consider each of the reviews carefully and submit a revised version along with a point-to-point response.

Best regards,
Yuan Shen
Associate Editor

Dear Dr. Chen et al.,

The revised version of your manuscript was re-evaluated by the previous three referees. While the reviewers have acknowledged the effort you put in revising the manuscript, all reviewers indicated that the revisions have addressed mainly their minor comments; their major concerns still remain unaddressed. For example, Referee #1 thought that this revision did not address the fundamental concern regarding the evidence that supports land use vs. channel slope as the major driver of DOC chemistry and source in the rivers, and the discussion text also needs to be reorganized and streamlined. Referee #2 pointed out again that the SUVA254 data were not consistently corrected (error remains in this version of the manuscript) and suggested to restructure the results/discussion. Referee #3 felt that the methodological shortcomings and the lack of sufficient methodological details after requesting the authors to address in the first review are still concerning. He/she also felt that the discussion is disjointed and in some places is sloppily done (i.e., trends are sometimes referred to and discussed as being opposite what the results show). Some of the results and conclusions (i.e., that DOM optics and isotopes are separately driven by land-use and geomorphology, respectively) are conflicting to numerous other works, which is not addressed or acknowledged.

Since all reviewers raised similar concerns and issues on this revision, I find it quite concerning. However, I agree with one of the reviewers that the data and findings of this study, if presented/discussed properly, could potentially be of interest to a broad community. I am therefore returning the manuscript for you to perform another round of MAJOR revisions. However, I would like to kindly bring to your attention that if the next revision features only marginal improvements and still fails to address the major concerns identified by the reviewers, the manuscript is likely to be rejected.

Reviewer comments are appended below for your reference. I look forward to seeing a much more improved revision.


Best regards,
Yuan Shen
Associate Editor

Referee #1:
Thank you for addressing many of technical comments and concerns from myself and the other reviewers. While the methods and statistical significance of the study results are clearer in this latest draft, the major contributions of this study remain difficult to follow because of the multitude of figure panels through the main text, the dense discussion, and the unnecessary inclusion of some previously published data. I suggest that the authors streamline the discussion text to focus on how the measurements made in the study can be used to build evidence in support of channel slope or land use as the major driver of DOC chemistry in the mountainous rivers, which is the main goal of this study. These types of revisions could help the authors identify which results to highlight in the discussion and which figure panels could be moved to the SI, which would improve the readability of the manuscript.

One aspect of the paper that remains feeble is the back and forth between channel slope and land use as potential major drivers of DOC cycling in the mountainous rivers in this study. Both of these factors could be driving the changes in DOC chemistry that were measured, but a discussion of which one might be more important is lacking. Likewise, if the authors cannot rule out one or the other, it is not admissible to say that both factors are driving DOC cycling because it is still possible that one factor is more important than the other. I suggest that the authors start the discussion by walking through the lines of evidence in support of one or the other. Without this type of critical analysis, it is difficult to believe that channel slope alone drives DOC concentration, which is the focus at the start of the discussion, and it is confusing to then read later in the discussion that land use is also a major driver. If there isn’t strong enough evidence to support one explanation over the other, then the authors should discuss why they cannot be teased apart rather than saying that both channel slope and land use drive DOC chemistry.

For example, the authors report that agricultural activities become more prominent going downstream, while at the same time channel slope generally decreases. This type of result makes me wonder whether there is a significant negative correlation between the % of urban and agriculture land use and the channel slope. Including a figure showing the % of urban and agriculture land use plotted versus the channel slope (even adding it as a panel to Fig. S1) would help readers to understand how correlation may not mean causation for this dataset, but that additional chemistry measurements (like the ones the author made) are needed to tease apart the major controls.

The authors include many measurements of water and DOC chemistry in the manuscript, but not all are needed for the authors to arrive at the main conclusions of the study. Including all the results obtained in the study in the main text makes it difficult to follow which figures best show the main results of the study and which are distracting to the reader. For example, past work by the authors in Chen et al. (2021) showcase only the figures needed to arrive at the main conclusions of the paper and it is much easier to follow. As the discussion reads right now, it is difficult to identify which chemistry measurements are being used to support the main findings of the paper and follow why the water chemistry previously published in Chen et al. (2021) are needed to support the main findings.

Other comments:
- Given that DOC concentrations decrease with distance downstream, similar to what the authors previously found for DIC and POC in Chen et al. (2021), wouldn’t it be more likely that DOC concentrations are also driven by groundwater or erosion rather than agricultural activities?
- It seems that comments about incorrect SUVA254 values have not been addressed in the current paper. The range of SUVA254 values on the y-axis of Fig. 6a should be the same as those reported in the y-axis of Fig. 3e, but they are not. The range of values showed in Fig. 3e is consistent with what has been previously reported in the literature, which makes me think that there was an error in the calculation for SUVA254 in Fig. 6a. The authors should check their spreadsheets to make sure that SUVA254 was calculated correctly in the files used to generate these figures. The authors could also report in the methods which final units for SUVA254 were obtained. They should be in units of L mg-C-1 m-1 using the decadic absorption coefficient at 254 nm.
- Line 101: How was annual air temperature obtained from ArcGIS? It seems to me that this should be reported separately from the physical catchment characteristics.
- Adding details about how the catchment slopes were estimated has improved the manuscript, but it would still be helpful to include a visual in the main text to show how the slopes vary within and between the rivers studied. Could you make another panel in Fig. 1 that shows channel slope on the y-axis versus distance in meters downstream? It is difficult to use the gradients shown in Fig. 1b and dots in Fig. 1a to piece this together myself, so having a figure that clearly shows the gradients would be helpful, especially when readers interpret the results shown in Fig. 3.
- If discussing differences in water chemistry between the spring water and rivers does not help support or refute the roles of land use or channel slope as drivers, then does this need to be included in the main text?
- Some of the information reported in Fig. 4 could be inferred or grasped easily from what is shown in Fig. 3 – do you need all of these figures in the main text? Which are needed to arrive at the main points in the paper?
- Figure 7 does not seem to contribute to the main points of the paper, so this could be moved to the SI.


Referee #2:
This study assessed how geographic controls (elevation, temperature, and slope) and % anthropogenic land cover (urban/agriculture) influence DOC export and DOM composition from mountainous rivers. The data presented shows that increased %urban/agriculture cover in lower reaches (and shallower gradients) of these catchments results in higher DOC concentrations, where carbon isotopic signatures (13 and 14C-DOC) of DOC are more deplete, and DOM is less aromatic. I believe these findings are of interest to a broad community. I believe the manuscript would be suitable for publication once the comments below are addressed.

General Comments:
1. The final paragraph of the introduction (aim/objectives) should be revised, as it is a little unclear as it stands. Specifically, I suggest combining the two hypotheses sentences into one to make the hypothesis clearer (i.e., by dealing with DOC concentration and quality at the same time).
Lines 93-5 is a list of metrics/relationships examined but the sentence is long and could do with
being broken up. I would also mention analysis of 14C-DOC samples in the Yinjiang river as a
separate point.
2. Section 3.1 – there is a tendency to only reference 2 out of 3 of the rivers in this section. I
understand why this is the case in some places as you are looking at where there are the largest
differences, but this could be made clearer.
3. Results section: many of the figures are discussed out of order in text, and there is a lot of
jumping between boxplots figures and then linear regressions. I suggest you restructure the
results to that there is an initial description of metrics across sites (i.e., geochemical, DOC,
isotopes, optical), followed by an additional section on the regressions with slope and land use. I think this will make the results easier to follow. Because of this, it would be good to include a
section briefly describing optical parameters before diving into covariance with slope/land use.
Consider including Figure S4 as a main text figure to aid initial description of optical metrics. This figure could be combined with Figure 7 and moved earlier in text. I would also suggest you
discuss optical indices (e.g., SUVA, FI, HIX) before describing PARAFAC results.
4. SUVA254 values have been corrected (i.e., in rebuttal table, and figure 3e), but not consistently (i.e., Figure 6a). Please update the figure and confirm that there is still a correlation with urban/agricultural land use.
5. 434 – 447 seems out of place. I think it would be better to contextualizes values more briefly
and earlier in the discussion or within the results section. The importance of table 3 is also
unclear to me.

Line Specific:
37: this sentence seems to be missing an ‘and’ or ‘as well as’
53-55: this is a little unclear consider rewording.
58: consider revising to “…, the underlying mechanisms that regulate DOC dynamics in small
mountainous rivers remain poorly understood’.
63: SOC has not been defined. Please check that abbreviations are always defined in text (same applies to OC on line 144, and TP)
64: ‘effectiveness’ seems like the wrong word choice here.
71-70: suggest making the difference in DOM quality between the two stream types clearer in this sentence.
100: consider abbreviating or including abbreviation throughout text.
104: ‘greatest’ rather than ‘great’.
111: revise sentence. Perhaps… “The proportion of urban and agricultural land uses in the Yuqing River catchment is from 17.3% to 23.1% (Figs. 1c and S1c). This catchment has typically higher % urban/agriculture land use than other studied catchments, and less variability in land use compared to Yinjiang and Shiqian river catchments (4.5% to 46.5% and from 9.6% to 41.3%, respectively).”
113: remove “typically”.
117: ‘respectively’ needs moving earlier in the sentence, just after values.
125: where were springs samples taken?
126-128: consider revising this sentence – it is a little unclear.
133: were bottles acid-washed before use?
135: what filter size was used for DIC? This should be specified.
136: remove ‘moreover’.
146: which analysis does the deviation relate to?
155: remove ‘same methods as 14C-POC’. The POC data was previously published? This should be made clearer in aims/objectives (i.e., after line 88), and perhaps reference should be made in figure captions.
157: I suggest stating that optical analyses were only conducted on River samples
199: can you contextualize which values represent supersaturation?
199: Q river also had higher water temperature than Y and springs?
224: add ‘although not significantly different.’
225: sentence seems incomplete – perhaps add ‘…besides groundwater to the rivers’
226: remove ‘in the supplement.’
285-286: it is unclear how a greater proportion of C3 in S and Q make them ‘distinctive’ to Y, especially when this is only significant for Y-S.
301: it would be useful to specify the direction of trends here.
298: your data does not support that this OC was ‘fresher’, as you did not find a significant correlation between freshness index and slope (lines 300)
316: there is more not ‘less’ aromaticity in steeper catchments.
317: there seems to be words missing from this sentence. Aromatic content tends to decline with what?
325: change to ‘….in regulating DOM composition.’
331: add ‘…increase in DOC concentration with microbial degradation in spring water…’
334: I think it would be useful to relate this back to the trends seen in your data.
352: replace ‘it is worth noting that’ with ‘furthermore.’
365: I agree, but I can’t see this trend in figure S3. There doesn’t seem to be a correlation between
elevation and land use or Cl- plotted.
379: I am unclear as to how you concluded that lower del13C-DOC with nitrate indicates greater algae contributions when no isotopic values for algae are presented. Some literature shows that algae has very enriched del13C values. Please expand and use isotopic data from the literature for endmembers to evaluate this discussion point.
399:’we further discussed’ is confusing here.
408: it would be useful to include values from your study here for context.
421: consider rephrasing
423: if there are significant damming/reservoirs on these rivers I think it would be useful to reference this in the site description
431: this sentence could be made clearer. I think you are point to the fact that it is difficult to
disentangle the two influences and they likely affect DOC concentration and DOM quality in tandem in these rivers.
454: ‘deeper’ is not needed
463-464: this seems like repetition.
Figure 2: please include Cl- concentrations as a panel.
Figure 2 / 7: ‘average’ should be replaced with ‘mean’ in the caption.
Figure 6: if PARAFAC components identified in the 3 rivers then why is there only one rivers data shown in panels b and C and/or why has the coloring changed. why is C3 not plotted in figure 6?
Figure 7: why are axes on EEMS not labelled. Please label axes and remove from caption.
Figures: boxes around legends are not always present – see comment from first review.

Referee #3:
I appreciate the authors' time and effort revising the manuscript substantially and addressing reviewer comments. While some of my concerns have been addressed, some of the methodological details provided are problematic and many details are still lacking. I believe that the authors need to provide significantly more details on their analyses and potentially revise their analyses/measurements to match standard protocol. Some issues (i.e., the lack of any bottle acid-washing or pre-combustion for DOC) I am not sure can be rectified at this point. Finally, there are some inconsistencies in the interpretation of trends in the discussion (see specific comments below).

Methodological concerns:

1- Sample bottles in which DOM are stored prior to analysis should be acid-washed (for plastic) or pre-combusted at 450°C for at least six hours for borosilicate glass (Mannino et al., 2019; Chow et al., 2022) to remove any organic carbon on bottle walls that can contaminate samples, especially when concentrations are as low as they are in this system. It is not acceptable to milli-Q rinse sample bottles for DOM without any acid-washing or baking, and I have never seen DOM work that does not pre-clean their sample bottles using acid or combustion. This is especially true when conducting isotopic analysis including radiocarbon.

2- The authors have provided no information on how catchment characteristics were calculated, only stating that it was calculated in ArcGIS. What data products were used (e.g., for land-use and for watershed boundaries)? What specific methods? Did you delineate sub-basin boundaries above each riverine sampling point and use that to calculate land-use? What reach length was used to calculate slope? This is the level of detail that is needed.

3- I am not sure where the a254 threshold value of 0.1 cm-1 for inner-filter correction cited by the authors comes from, as it is not from Kothawala et al. (2013). According to Kothawala et al. (2013), inner-filter correction should be conducted when the sum of the absorbance of the excitation and emission wavelengths is greater than 0.05 cm-1. This was not tested by the authors to determine whether or not they needed to perform inner-filter correction. However, based on the presented a254 values, which averaged around 0.04 cm-1 (for a single wavelength), it seems likely that inner-filter correction would need to be performed once accounting for the sum of both excitation and emission wavelengths. Substantial changes to fluorescence data, and therefore, PARAFAC results, can occur if not correcting for absorbance (see Kothawala et al., 2013, Fig. 2), which can be especially problematic if absorbance varies across samples (as it does in this study), because differences in absorbance could be driving observed differences in fluorescence.

4- The radiocarbon description here and in the cited paper with more detailed methods contains no information on how the samples for radiocarbon measurement were stored and for how long, and how they were processed following measurement (for example, were ∆14C values corrected for fractionation using 13C?) I appreciate the authors additional information around the radiocarbon measurement 14C/12C background ratio, and I think the Dong et al. 2018 citation should be included when measurement on the AMS is mentioned (Ln 155-156): “…and measured by an accelerator mass spectrometry (AMS) system with an analytical error of ±3‰.” However, I was referring to whether procedural blanks were conducted when processing the samples using wet chemical oxidation – a good example of this is Xu et al. (2021) (for UV oxidation), and I would argue this is necessary and should be standard practice whenever processing samples for radiocarbon using wet chemical oxidation. Please see Haghipour et al. (2019) for an example of how to use procedural blanks or standards to correct for contamination when processing samples using wet chemical oxidation.

In general, please include as much information as possible on sample handling, storage conditions, etc. for all measurements performed.

Other comments:

Autochthonous DOM introduced in the introduction but not defined.

The organization of the introduction is very confusing – it needs a cohesive structure. I suggest the authors first define DOM and explain why it’s important (this is mostly already done in the first paragraph). Then explain DOM source (allochthonous vs. autochthonous) and explain how source relates to DOM composition generally. Then explain how and why DOM source and composition might vary by geographic controls (elevation, slope, temperature) and land-use (agriculture, urbanization). End with your hypotheses/predictions based on what you have laid out in the earlier paragraphs.

Ln 89-91: “We further hypothesize that there will be a large difference on DOM quality and carbon isotopes between these catchments and those with less influences by agricultural and urban land uses but steeper channel slopes and higher elevation” What kind of differences?

Table S1: I would suggest moving this to the main text in the methods so that it is easy to see what the different components represent.

Figure 6a: SUVA values are the previous incorrectly-calculated values

Figure 2: Why are ∆14C -DOC and -POC not included, given that spatial variations are discussed?

Figures 4-6: I don’t really understand the organization of these figures. For example, why was 13C-DOC vs. NO3-N included in Figure 4, which seemingly seems to be all related to DOC amount and anthropogenic impact? There are a lot of indices/relationships to keep track of, and I wonder if a principal component analysis would visually be easier to follow (and driver wise easier to make sense of)?

Ln 234: “Unlike DOC, a strong negative correlation with mean channel slope was found for δ13CDOC (Fig. 3b)” There was a strong negative correlation for DOC concentration, and a positive correlation for 13C-DOC – is this a typo?

Ln 283: “Authochthonous” spelling typo

Ln 287: Specify that you are referring to C1 and C2 percentage, not amount

Ln 311-312: “Furthermore, aged DOC in river systems has been attributed to old soil organic matter in deeper layer input into rivers through deeper flow paths (Barnes et al., 2018; Masiello and Druffel, 2001).” Revise this sentence for clarity

Ln 315: “The correlation of SUVA254 with mean channel slope suggests that steeper catchments tend to export DOC with less aromaticity (Fig. 3e), indicating the geomorphologic effects on DOM characteristics (Harms et al., 2016).” This is not consistent with what your data are showing, which is that SUVA is higher in high relief areas (so more aromatic). How would you interpret this?

Ln 328-334: It is unclear how this relates to your results.

Ln 348: Mention that the groundwater is “spring” in Fig 2d

Ln 335-351: I appreciate the thorough analysis regarding the contributions of groundwater, but I think you can shorten this paragraph a bit given that it turns out the groundwater is not an important source of DOC

Ln 352-358: I agree, however, your results do not really point to greater contributions of terrestrial DOM in the low relief areas – there is an increase in C1 the microbial component downstream, but a decrease in SUVA, and relatively little change in the freshness index or HIX. Maybe comparing the absolute value of the PARAFAC components (i.e., in Raman Units rather than percent) you could see if C3 increases in low relief compared to high relief (suggesting that the amount of terrestrial DOC input increases)?

Ln 426: “This may have significantly influenced the organic carbon dynamics in the study rivers (Chen et al., 2021).” Can the authors elaborate on damming and reservoirs in this system? This seems like an extremely important point that was not addressed here.

Conclusions: Could you provide some explanation for why DOC age and optical properties are showing such different drivers? Other work would suggest that these should be highly related (Butman et al., 2012), and it seems odd that agriculture would influence the optics but not radiocarbon and the geomorphology vice versa.

Review References:
Butman, D., Raymond, P. A., Butler, K., and Aiken, G.: Relationships between Δ 14 C and the molecular quality of dissolved organic carbon in rivers draining to the coast from the conterminous United States, Global Biogeochemical Cycles, 26, 2012GB004361, https://doi.org/10.1029/2012GB004361, 2012.

Chow, A. T.-S., Ulus, Y., Huang, G., Kline, M. A., and Cheah, W.-Y.: Challenges in quantifying and characterizing dissolved organic carbon: Sampling, isolation, storage, and analysis, Journal of Environmental Quality, 51, 837–871, https://doi.org/10.1002/jeq2.20392, 2022.

Haghipour, N., Ausin, B., Usman, M. O., Ishikawa, N., Wacker, L., Welte, C., Ueda, K., and Eglinton, T. I.: Compound-Specific Radiocarbon Analysis by Elemental Analyzer-Accelerator Mass Spectrometry: Precision and Limitations, Analytical Chemistry, 91, 2042–2049, https://doi.org/10.1021/acs.analchem.8b04491, 2019.

Kothawala, D. N., Murphy, K. R., Stedmon, C. A., Weyhenmeyer, G. A., and Tranvik, L. J.: Inner filter correction of dissolved organic matter fluorescence: Correction of inner filter effects, Limnol. Oceanogr. Methods, 11, 616–630, https://doi.org/10.4319/lom.2013.11.616, 2013.

Mannino, A., Novak, M. G., Nelson, N. B., Belz, M., Berthon, J.-F., Blough, N. V., Boss, E., Bricaud, A., Chaves, J., Del Castillo, C., Del Vecchio, R., D’Sa, E. J., Freeman, S., Matsuoka, A., Miller, R. L., Neeley, A. R., Röttgers, R., Tzortziou, M., and Werdell, P. J.: Measurement protocol of absorption by chromophoric dissolved organic matter (CDOM) and other dissolved materials, IOCCG Ocean Optics and Biogeochemistry Protocols for Satellite Ocean Colour Sensor Validation, 1, 1–77, 2019.

Xu, L., Roberts, M. L., Elder, K. L., Kurz, M. D., McNichol, A. P., Reddy, C. M., Ward, C. P., and Hanke, U. M.: RADIOCARBON IN DISSOLVED ORGANIC CARBON BY UV OXIDATION: PROCEDURES AND BLANK CHARACTERIZATION AT NOSAMS, Radiocarbon, 63, 357–374, https://doi.org/10.1017/RDC.2020.102, 2021.

Dear Dr. Chen et al.,

Thank you for submitting the revised manuscript, which has been seen by three referees. The reviews are appended below. Comments from reports 2 and 3 are mostly specific points and easy to address. I would like to bring your attention to report 1, where there are still important concerns about the unclear methods, exhaustive results, and unfocused discussion. I invite you to make proper changes to clarify these issues.

Best regards,
Yuan Shen
Associate Editor

Report #1:
This manuscript describes relationships between riverine organic carbon concentration and quality in three mountainous catchments. The authors highlight the importance of catchment slope and anthropogenic land use as important factors affecting these organic carbon properties, and cite the literature extensively to support their hypotheses. There is a lot of interesting data collected and summarized, which is useful for comparisons with mountain stream and river ecosystems globally.

Three major issues with the manuscript in its current form:
1) Even after several comments from previous reviewers, there remains some concerns about the methods employed and a lack of description in some cases. Additionally, with such multivariate data, it is concerning that the authors rely solely on univariate statistics. The complicated and sometimes overwhelming interpretation of linear regressions could be simplified with multivariate approaches.
Some specific issues in the Methods:
Line 131: “Annual air temperature…[was] determined using ArcGIS.” Perhaps this is in reference to a specific data layer, but as written it is unclear.
Line 136: Description of carbonate rocks suggests weathering rates could be high, but the impact of this on carbon ages is not thoroughly discussed.
Line 139: What is the spatial distribution of soil organic carbon or soil depth? No data on soil properties is described despite likely being the most important source of organic carbon to the streams.
Line 147: Runoff units would be helpful, either instead or additionally.
Line 152: Time of year of sampling is likely very important, but is not discussed later.
Line 161: How long were samples stored?
Line 170: Is this true for all samples?
Line 172: Relative deviation of what? Did you take replicate field samples? Lab samples? This a concern for several analyses, i.e., if duplicates were taken, and if so, what kind of duplicate was measured.
Line 178: Which 9 samples? Is that all of the samples from the Yinjiang River? If not, why were they chosen?
Line 186: At what interval?
Line 196: Is there any concern about DOM properties changing in 1 week?
Line 215: If you are doing all of these correlations, how do you determine what is “predominant?” Anything significant? Do you have concerns about doing so many univariate analyses?
Line 220: A mean is not necessarily representative if you are working with small sample sizes and non-normal data.
Line 221: Sometimes removing and sometimes including a data point seems difficult to defend without a specific metric.
Line 302: Anthropogenically derived chloride is not defined in the text.

2) The Results are exhaustive, and as a result, quite unfocused. It is unclear which results are important to the central message of the manuscript. This is indicative of a lack of clear focus within the entire manuscript. As previous reviews have pointed out, there are a lot of figures and tables. I would agree, and suggest that most of these figures are relatively simple and do little else than to show correlation. Some higher-level analysis or results would be greatly beneficial, including some multivariate approaches.

3) The Discussion section is written in a way that does not clearly differentiate what are interpretations of this study and what are supporting ideas from other studies. Perhaps this is because the interpretation is complex, but the authors do not clearly establish what are their main conclusions or interpretations. Line 474 is telling, “disentangling the dual influences…is challenging.” The results do not accomplish this, the discussion does not do much to clarify either. But the analysis is perhaps what is most limiting, in which univariate statistics are repeatedly used to approach a complex and multivariate problem. The repeated interpretation of correlation as causation is also problematic. Additionally, while the authors mention how land use and slope are not independent variables towards the end of the discussion, this should be a major caveat and approached more thoroughly early in the manuscript.


Report #2:
- There are some contradicting statements of how DOM chemistry change with elevation between lines 59-62 and lines 66-69. Do you use these examples to show that there are differing results in past studies?
- Line 86: There are other papers you can cite here as well on DOM lability in agricultural streams and under high nutrient loads
- Line 417: I'm guessing this should say DOM characteristics


Report #3:
The manuscript here explores how geographical and anthropogenic factors impact DOM abundance and composition. This topic is important in global carbon cycling, especially under the scenario of climate change and intensified anthropogenic activities. However, here are some specific comments which should be addressed before acceptance.
Specific comments:
L56-57 The authors should check this sentence for grammar and logic issues: “Recent studies have shown that geographical (e.g., elevation and catchment slope) controls on DOC export may also be important for riverine carbon cycling (Connolly et al., 2018; Li Yung Lung et al., 2018).”, and also the reference format here “Li Yung Lung et al., 2018”.
L59: “characterized by greater releases of DOC”, what does this mean? “Release of DOC”, from where or to where? “Greater releases”, the quantity or the flux or the rate?
L60: “protein-like fluorescence DOM” should be “protein-like fluorescent DOM”.
L134: The authors should check the value of the slopes (“mean catchment slope (from 14.3° to 25.5°)”. Is the magnitude right? Not one order less? I’m not familiar with this, however, it should be one order less considering the spatial scale (30-60 km) and the altitude difference (about 2 km).
L189-190: The authors should check the definition of a254 and A254, and also the unit of absorption coefficients. The definition and calculation of absorbance (A254) and the absorption coefficient (a254) could refer Hu et al. (2002) and Li et al. (2017). Meanwhile, commonly the unit of a254 is m-1, not cm-1.
Ref: Hu C, Muller-Karger F E, Zepp R G. Absorbance, absorption coefficient, and apparent quantum yield: A comment on common ambiguity in the use of these optical concepts[J]. Limnology and Oceanography, 2002, 47(4): 1261-1267.
Li P, Hur J. Utilization of UV-Vis spectroscopy and related data analyses for dissolved organic matter (DOM) studies: A review[J]. Critical Reviews in Environmental Science and Technology, 2017, 47(3): 131-154.
L194-206: Have the authors considered the inner filter correction for fluorescence data?
L225: The authors should check the definition and calculation of SUVA254 in Table 2. In Weishaar et al. (2003), they use A254, not a254.
L225: Will the authors consider the updated calculation and interpretation of fluorescence index (FI)? FI = Em470/Em520, at Ex 370 nm. The authors could refer to the updated reference (Cory R M, Miller M P, McKnight D M, et al. Effect of instrument‐specific response on the analysis of fulvic acid fluorescence spectra[J]. Limnology and Oceanography: Methods, 2010, 8(2): 67-78.).
L229: “between” or “among”?
L278-279: The term used here should be consistent with Figure 3. What does FI mean here? Fluorescence index? Then it should be related to Figure 3b according to the Y label of Figure 3b. But the authors related FI here with Figure 3d (“FI of DOM ranged from 1.66 to 1.94, averaging 1.78 (Fig. 3d)”), while the Y label for Figure 3d is freshness index.
L294: The authors should provide the references to support/indicate why Cl- is anthropogenically derived here.
Figure 5: The box for legend did not display well.
Figure 5: As stated in the introduction part (L80-89) and L393-394, agricultural and urban land use exerted different impacts on DOM abundance and composition, why the authors combined these two landuse patterns to demonstrate the anthropogenic impacts, rather than separating these two to provide detailed explanation?
L352-354: Both geographical and anthropogenic factors influence the DOM abundance and composition. Here, the export of DOC with higher aromaticity may be due to the landuse pattern (Fig 7(a), and steeper catchments could be coincident. How to differentiate these factors here?
L366: “increasing DOC concentrations … due to microbial degradation”? Please check the logic.
L401-402: The authors should provide more details for this statement “anthropogenic impacts can also decrease DOC concentrations”. How?
L428: “consistent with previous studies”, how to explain this pattern?
L451-453: If “the weak positive correlation …indicated that DOC and POC may have been derived from the same source”, what does the strong positive correlation indicate? The authors could rephrase this sentence to avoid ambiguity.

Dear Dr. Chen et al.,

Thank you for submitting the revised manuscript, which has been seen by three referees. The reviews are appended below. Comments from reports 2 and 3 are mostly specific points and easy to address. I would like to bring your attention to report 1, where there are still important concerns about the unclear methods, exhaustive results, and unfocused discussion. In particular, they thought that the manuscript fails to engage the data deeply. An over-reliance on univariate correlation and descriptive analyses makes interpretation difficult and possible misleading - the two main questions, catchment slope and land use are correlated to begin with. Additionally, the Methods remain questionable in parts, which has been pointed out by previous reviewers already. Finally, the Discussion is written in a way that does not differentiate clearly the results of this analysis and other papers, and fails to highlight key takeways.

Overall, while the manuscript has gone through several revisions, major concerns related to the methods, results and discussion have not been fully addressed. I suggest the authors to make a solid effort to address these issues in the next revisions.


Best regards,
Yuan Shen
Associate Editor

Report #1:
This manuscript describes relationships between riverine organic carbon concentration and quality in three mountainous catchments. The authors highlight the importance of catchment slope and anthropogenic land use as important factors affecting these organic carbon properties, and cite the literature extensively to support their hypotheses. There is a lot of interesting data collected and summarized, which is useful for comparisons with mountain stream and river ecosystems globally.

Three major issues with the manuscript in its current form:
1) Even after several comments from previous reviewers, there remains some concerns about the methods employed and a lack of description in some cases. Additionally, with such multivariate data, it is concerning that the authors rely solely on univariate statistics. The complicated and sometimes overwhelming interpretation of linear regressions could be simplified with multivariate approaches.
Some specific issues in the Methods:
Line 131: “Annual air temperature…[was] determined using ArcGIS.” Perhaps this is in reference to a specific data layer, but as written it is unclear.
Line 136: Description of carbonate rocks suggests weathering rates could be high, but the impact of this on carbon ages is not thoroughly discussed.
Line 139: What is the spatial distribution of soil organic carbon or soil depth? No data on soil properties is described despite likely being the most important source of organic carbon to the streams.
Line 147: Runoff units would be helpful, either instead or additionally.
Line 152: Time of year of sampling is likely very important, but is not discussed later.
Line 161: How long were samples stored?
Line 170: Is this true for all samples?
Line 172: Relative deviation of what? Did you take replicate field samples? Lab samples? This a concern for several analyses, i.e., if duplicates were taken, and if so, what kind of duplicate was measured.
Line 178: Which 9 samples? Is that all of the samples from the Yinjiang River? If not, why were they chosen?
Line 186: At what interval?
Line 196: Is there any concern about DOM properties changing in 1 week?
Line 215: If you are doing all of these correlations, how do you determine what is “predominant?” Anything significant? Do you have concerns about doing so many univariate analyses?
Line 220: A mean is not necessarily representative if you are working with small sample sizes and non-normal data.
Line 221: Sometimes removing and sometimes including a data point seems difficult to defend without a specific metric.
Line 302: Anthropogenically derived chloride is not defined in the text.

2) The Results are exhaustive, and as a result, quite unfocused. It is unclear which results are important to the central message of the manuscript. This is indicative of a lack of clear focus within the entire manuscript. As previous reviews have pointed out, there are a lot of figures and tables. I would agree, and suggest that most of these figures are relatively simple and do little else than to show correlation. Some higher-level analysis or results would be greatly beneficial, including some multivariate approaches.

3) The Discussion section is written in a way that does not clearly differentiate what are interpretations of this study and what are supporting ideas from other studies. Perhaps this is because the interpretation is complex, but the authors do not clearly establish what are their main conclusions or interpretations. Line 474 is telling, “disentangling the dual influences…is challenging.” The results do not accomplish this, the discussion does not do much to clarify either. But the analysis is perhaps what is most limiting, in which univariate statistics are repeatedly used to approach a complex and multivariate problem. The repeated interpretation of correlation as causation is also problematic. Additionally, while the authors mention how land use and slope are not independent variables towards the end of the discussion, this should be a major caveat and approached more thoroughly early in the manuscript.


Report #2:
- There are some contradicting statements of how DOM chemistry change with elevation between lines 59-62 and lines 66-69. Do you use these examples to show that there are differing results in past studies?
- Line 86: There are other papers you can cite here as well on DOM lability in agricultural streams and under high nutrient loads
- Line 417: I'm guessing this should say DOM characteristics


Report #3:
The manuscript here explores how geographical and anthropogenic factors impact DOM abundance and composition. This topic is important in global carbon cycling, especially under the scenario of climate change and intensified anthropogenic activities. However, here are some specific comments which should be addressed before acceptance.
Specific comments:
L56-57 The authors should check this sentence for grammar and logic issues: “Recent studies have shown that geographical (e.g., elevation and catchment slope) controls on DOC export may also be important for riverine carbon cycling (Connolly et al., 2018; Li Yung Lung et al., 2018).”, and also the reference format here “Li Yung Lung et al., 2018”.
L59: “characterized by greater releases of DOC”, what does this mean? “Release of DOC”, from where or to where? “Greater releases”, the quantity or the flux or the rate?
L60: “protein-like fluorescence DOM” should be “protein-like fluorescent DOM”.
L134: The authors should check the value of the slopes (“mean catchment slope (from 14.3° to 25.5°)”. Is the magnitude right? Not one order less? I’m not familiar with this, however, it should be one order less considering the spatial scale (30-60 km) and the altitude difference (about 2 km).
L189-190: The authors should check the definition of a254 and A254, and also the unit of absorption coefficients. The definition and calculation of absorbance (A254) and the absorption coefficient (a254) could refer Hu et al. (2002) and Li et al. (2017). Meanwhile, commonly the unit of a254 is m-1, not cm-1.
Ref: Hu C, Muller-Karger F E, Zepp R G. Absorbance, absorption coefficient, and apparent quantum yield: A comment on common ambiguity in the use of these optical concepts[J]. Limnology and Oceanography, 2002, 47(4): 1261-1267.
Li P, Hur J. Utilization of UV-Vis spectroscopy and related data analyses for dissolved organic matter (DOM) studies: A review[J]. Critical Reviews in Environmental Science and Technology, 2017, 47(3): 131-154.
L194-206: Have the authors considered the inner filter correction for fluorescence data?
L225: The authors should check the definition and calculation of SUVA254 in Table 2. In Weishaar et al. (2003), they use A254, not a254.
L225: Will the authors consider the updated calculation and interpretation of fluorescence index (FI)? FI = Em470/Em520, at Ex 370 nm. The authors could refer to the updated reference (Cory R M, Miller M P, McKnight D M, et al. Effect of instrument‐specific response on the analysis of fulvic acid fluorescence spectra[J]. Limnology and Oceanography: Methods, 2010, 8(2): 67-78.).
L229: “between” or “among”?
L278-279: The term used here should be consistent with Figure 3. What does FI mean here? Fluorescence index? Then it should be related to Figure 3b according to the Y label of Figure 3b. But the authors related FI here with Figure 3d (“FI of DOM ranged from 1.66 to 1.94, averaging 1.78 (Fig. 3d)”), while the Y label for Figure 3d is freshness index.
L294: The authors should provide the references to support/indicate why Cl- is anthropogenically derived here.
Figure 5: The box for legend did not display well.
Figure 5: As stated in the introduction part (L80-89) and L393-394, agricultural and urban land use exerted different impacts on DOM abundance and composition, why the authors combined these two landuse patterns to demonstrate the anthropogenic impacts, rather than separating these two to provide detailed explanation?
L352-354: Both geographical and anthropogenic factors influence the DOM abundance and composition. Here, the export of DOC with higher aromaticity may be due to the landuse pattern (Fig 7(a), and steeper catchments could be coincident. How to differentiate these factors here?
L366: “increasing DOC concentrations … due to microbial degradation”? Please check the logic.
L401-402: The authors should provide more details for this statement “anthropogenic impacts can also decrease DOC concentrations”. How?
L428: “consistent with previous studies”, how to explain this pattern?
L451-453: If “the weak positive correlation …indicated that DOC and POC may have been derived from the same source”, what does the strong positive correlation indicate? The authors could rephrase this sentence to avoid ambiguity.

Dear Dr. Chen et al.,

Thank you for your efforts in making significant revisions, which I believe have addressed most of the concerns raised by the reviewers. I trust you found this process valuable for enhancing your manuscript. Your responses to comments and the corresponding revisions, especially in method descriptions, the application of new statistical approaches, and the consolidation of text and figures, are mostly on target and have enhanced the clarity and quality of these revisions.

Upon reviewing this version, I noticed a few minor changes that need attention:

Regarding the computation of SUVA254, it is accurate to utilize the decadic term of absorbance (i.e., absorbance normalized to path length, measured in m-1) for SUVA254 calculations, following the method outlined in Weishaar et al. 2003. However, in this context, the symbol representing the decadic absorption coefficient is italicized alpha (α), not the letter a. The letter a (or more often in its italic form) is typically employed to denote the Napierian absorption coefficient, where a is equal to α times ln10. To align with the correct notation, the authors can simply substitute the term "a254" with "α254" (alpha α in its italicized form) in equation (1) and add "decadic" before "absorption coefficient" in the subsequent line.

line 273: remove “were” in the title of Table 2.

line 272: define “SD”. I assume it stands for Standard Deviation.

lines 298-324: Section 3.3, I think it would be more informative to report r values in addition to p values. The r values help evaluate the strength and direction of the correction described in the text.

line 348: Figure 6 is of low resolution; the text appears blurry.

line 383: 2014 should be 2015.

line 465: Suggestion: insert “compiled and” before “shown”

line 499: Regarding the statement on the availability of data, please refer to our data policy (https://www.biogeosciences.net/policies/data_policy.html). Authors are required to provide a statement on how their underlying research data can be accessed. If the data are not publicly accessible, a detailed explanation of why this is the case is required. The best way to provide access to data is by depositing them (as well as related metadata) in FAIR-aligned reliable public data repositories, assigning digital object identifiers, and properly citing data sets as individual contributions.


Best regards,
Yuan Shen
Associate Editor

Dear Dr. Chen et al.,

Thank you for incorporating the final revisions. Considering the enhancements made and the quality of the current version, I am pleased to accept your manuscript for publication in Biogeosciences.


Thank you for submitting your work to Biogeosciences.

Best regards,
Yuan Shen
Associate Editor