Review of the paper “Multidecadal trends in CO2 evasion and aquatic metabolism in a large temperate river” by An Truong Nguyen et al.

This paper is focused on a timely and relevant question, which is to better under how fluvial ecosystems regulate the global C cycle. The data set, with more than three decades of data, is unique not only because of its length but also because there are very few high temporal resolution data of this quality in large rivers. I sincerely congratulate the authors for their vision and perseverance to put together this impressive data set. Moreover, the paper reports interesting results illustrating that rivers can act either as sources or sinks of carbon, and that this pattern can change seasonally but also at large time scales depending on the nutrient status of the ecosystem. This finding has important implications for understanding how fluvial networks work and their contribution to global C fluxes under present and future anthropogenic pressures. Overall, I think this research will be of interest to the audience of Biogeoscience, though the paper requires major changes to improve clarity and streamline data analysis and the interpretation of the results before publication. Below, I provide some general and specific comments and suggestions, which I hope will be of help to the authors when crafting the revised version of the paper.

General comments

Long-term trends in groundwater CO2 inputs. One of my main concern is about long-term changes in groundwater CO2 inputs. As mentioned by the authors, it seems that the observed long-term decrease in FCO2 is mostly associated with a decrease of about 50% in groundwater inputs between the phytoplankton dominated and the macrophytes dominated periods. How reasonable this is? At the very end of the discussion, the authors suggest that there has been a generalized decrease in groundwater CO2 fluxes in the Loire catchment. Yet, it is not clear whether the long-term trend in discharge data support this explanation. How reasonable is to think that CO2 concentrations in groundwater have change if there have not been large changes in groundwater levels, neither in weathering rates. Overall, this flux is highly uncertain, and difficult to constrain with independent data.  

Re-oligotrophication. This phenomenon becomes crucial for understanding the temporal patterns in stream metabolic activity and CO2 sources, yet the magnitude of change of nutrients and DOM in the study river over time is barely mentioned. Even if this shift in water chemistry has been explained in a previous paper, some more quantitative information will help to better framed the discussion and interpretation of the results of this paper.

Terminology. The authors use many different concepts to describe whether their system is dominated by macrophytes or phytoplankton, whether it is in an oligotrophic or eutrophic state, and finally classify the system behavior in four trophflux states as a function of CO2 fluxes and metabolic activity, which is the cornerstone of the results. For instance, “macrophyte-dominated” and “oligotrophic” regimes as well as “phytoplankton-dominated” and “eutrophic” regimes are used at the beginning. Also, the authors refer to “regime”, “states”, or “periods” non-consistently when referring to either “trophic conditions” or to metabolic activity. Overall, my suggestion is to simplify a bit this terminology and make sure to refer always in the same terms to the same concepts. For instance, only use either macrophyte- vs phytoplankton-dominate OR oligotrophic- vs eutrophic- regimes, and be consistent referring to either “states”, “regimes”, or “periods”.

Metabolic stoichiometry to convert O2 to CO2 moles. More details on these calculations are needed. An important aspect is whether conversions were similar for the phytoplankton- and the macrophyte- dominated periods, and to discuss the uncertainty associated with these calculations.

Change point analysis and statistical analysis. Is this analysis important enough to keep it in the main manuscript? At the end of the day, the authors are splitting the data set per decades. While I agree that the changepoint analysis somehow supports to split the data like by decades, I wonder whether it might be enough to add this analysis in the supplementary materials. On the other hand, the results would be better supported if the authors use statistical tests to explore whether differences among periods (and/or states) for the different variables are statistically significant. This would help to more clearly distinguish the most remarkable changes, and avoid qualitative statements.

Internal vs external sources of CO2. While I understand the point of the authors, this is an oversimplification of CO2 sources. For instance, by referring to “external CO2 sources” the authors imply there is no other internal sources than aerobic metabolism producing CO2 in the study system. How reasonable is to assume that there is no anaerobic metabolism? The authors should include some rational about this assumption, or else refer to “Other sources” rather than to “External sources”. Regarding “internal sources”, I wonder whether diel signals of dissolved oxygen fully capture the metabolism associated with photoautotrophs. In Table 1, the authors report negative values for “external CO2 inputs” which seems unrealistic. A potential explanation could be a systematic underestimation of the photoautotrophic activity by either phytoplankton or macrophytes, which might be more evident during this state, though may be happening also during other states. On the other hand, how feasible is that “external inputs” vary so much among states within a given decade? The authors should better discuss and, if possible, constrain, this factor to the best of their knowledge.

Sources of uncertainty. The authors need to better consider in their calculations the different sources of uncertainty. The supplementary materials tackle some of these sources of uncertainty, but some of this rationale needs to be moved to the main text, and other additional sources of uncertainty such as those associated with respiration and photosynthetic coefficients, anaerobic respiration, k600 in large streams (note that Raymond equations are useful for small streams with complete water column mixing, which is not the case of large rivers), and GPP not captured by DO signals in the water column (which may happen for macrophytes) should also be considered.  

Contribution of internal sources to total CO2. Overall, I wonder whether it makes sense to report -NEP/FCO2 in all cases since the implications of the mass balance are quite different depending on whether the stream is acting as a source or a sink of CO2. In particular: (1) No doubt about what -NEP/FCO2 implies for the heterotrophic-CO2 source state; (2) For the autotrophic-CO2 source state, the contribution of the stream to FCO2 is actually 0%, and photoautrotrophs could contribute to reduce “external CO2 inputs” by xx % ( i.e. -NEP/external CO2 rather than -NEP/FCO2); (3) For the heterotrophic-CO2 sink state, it has no sense to me that groundwater is not contributing CO2, unless the stream is losing water, and in this case, there might be either an unaccounted pool fixing CO2 from the water column, or GPP is systematically underestimated for whatever reason; (4) For the autotrophic-CO2 sink state, the internal source could contribute to balance out 100% of the “external CO2 sources”, and contribute to fix additional CO2 from the atmosphere (i.e. not sure whether -NEP/FCO2 is really meaningful in this case). From a mass balance perspective, Figure 5 (in the discussion) makes much more sense than Table 1, and my feeling is that the manuscript would be more easy to follow if the results focus on the mass balances.

Specific comments

Abstract

L26-27. For (ii), not clear from this sentence whether the contribution of aquatic metabolism was higher or lower during the eutrophic or the oligotrophic trophic regime.  For (iii), better highlight the predominant role of the river as a source of CO2. For (iv), might be more informative to highlight the seasonality of FCO2, and how this was modulated by the trophic regime rather than referring to the hysteresis patterns.

L31.”dynamic within and across years” as a function of what? The amount of nutrients?

Introduction

L38. Better say “is assumed to come”, since there are already several published studies challenging this assumption.

L54-56. In which way these variables controlled by discharge (inputs of carbon and nutrients) would influence metabolic activity and the balance between GPP and ER?

L72-74. Clarify what do you mean by “positive NEP yields local organic matter increases”. Do you mean in the form of algal biomass? Increases in particulate and dissolved organic matter? Explain why “this autotrophic state” is most common in larger rivers, and clarify why “this is typically missed by FCO2 sampling campaigns”.

L75. Indicate if this finding is general to all large rivers, or if it was observed in specific rivers.

L81. For contextualization purposes, provide some information on how nutrient concentrations changed between the eutrophic and oligotrophic regimes and this phenomenon happen. It is also important to recall this in the discussion, to better interpret the large changes in both groundwater CO2 inputs and metabolic activity within the river.

L85. By the growing season do you mean spring and summer?

L83-87. These two sentences can be merged and shorten.

L88. Please, could you provide other examples of re-oligotrophication in developed countries? This shift towards lower nutrient concentration in large rivers is not so evident giving the modest improvements in water chemistry observed in the last decades in Europe.

L91-93. Note that the hypothesis is lacking the reasoning behind. Why did you expect an increase in the contribution of FCO2 from aquatic metabolism if, according to the earlier paragraph, you actually observed a decrease in NEP with reoligotrophication?

L94. Note that in the earlier paragraphs you refer to “regime” when talking about the trophic conditions, but to “states or periods” when referring to stream metabolic activity. To help the reader, better be consistent with the terminology throughout.

L96. How do you expect discharge to influence FCO2 in the first term? Would  FCO2 increase or decrease with discharge? Why will Q influence FCO2 differently in the macrophyte dominated period across seasons? And why this seasonal influence will not emerge in the phytoplankton dominated period?

Methods

L112. And during winters?

L130. How did you transform stream metabolic rates from O2 to C units? Which stoichiometric ratios did you use (i.e., photosynthetic and respiration coefficients). Did you consider whether these coefficients vary between the phytoplankton- and the macrophyte-dominated regimes?

L137. Only 12% of discards is a big success! Why did you choose to fill the gaps? Please, indicate in the main text whether main results and conclusions hold if not filling the gaps.

L139. I think Supplementary Section S2 is missing or, if it comes latter, Supplementary sections should be reordered to be cited in order in the main text.

L150-151. What do you mean by “river CO2 state compared over 32 years”? Do you mean that there were no long-term trends in concentration? That there were no statistically significant differences in average CO2 concentration between the two trophic regimes? Best used past tense.

L156. Delete “with” after “multiplying”.

L157. Add “the” between “with” and “seven”.

L161-165. To be formal, define all the terms included in these equation (depth and T).

L166.This subtitle is sort of funky. Something like “The trophlux categories” would be enough.

L167-169. Well, for NEP these states have been defined for decades. I think Odum reserves credit here.

L178. Could also the heterotrophic-sink state also occur during high discharges because of high gas exchange with the atmosphere?

L191. Explain briefly what is a seasonal decomposed time series.

L198-201. For the reader to follow this prediction the expectations need to be better explained in the last paragraph of the introduction.

L201-204. Please, provide some hints of how the two metrics used to characterize the hysteresis loops are expected to change between the phytoplankton vs macrophyte-dominated regimes.

Results

L210. Explain better this successive seasonal transition between autotrophic/heterotrophic of NEP, sink/source of FCO2.

L218-221. Would be helpful to include discharge in Figure 1. 

L222. Change “-“ by “to” between “-383” and “584” to smooth the reading (suggestion holds for the whole results section). Note that the units are expressed differently in the main text and in Figure 1 (y vs yr)

L224. Add “net” before “source”.

Figure 2. Honestly, pCO2, pH, alkalinity, and k600 could be moved to the supplementary.

L244-249. Better apply a statistical test for comparing average values for each period and variable.

L250. For the whole section and throughout the manuscript, would be more helpful to the reader if you refer to “heterotrophic-CO2 source” rather than to “heterotrophic-source”. Also, the text would flow better if you refer consistently to the 4 trophlux states throughout.

L255. Clarify whether this is the annual range or an average value for each decade, and if the later, provide s.e.

L256. “coinciding with low water temperature and high discharge”. This result is quite rough. Please use a two-way ANOVA test or similar to support this statement. Clarify whether the 90% refers to all data or to each decade.

L257-259. Bis as my earlier comment. If these are averages per decades, add the s.e., and clarify to which decade refer each number.

L260-261. This sentence is confusing. Moreover, two of the remaining three trophlux states act as sinks rather than sources of CO2, so why one would expect them to contribute to FCO2?

L261-263. Just refer to the occurrence of the autotrophic-CO2 sink state to follow the same logic throughout.

L263. Are these average values? Then add s.e.

L267. Say more clearly that this state represented a small sink of CO2.

Table 1. The caption should better explain the variables to make sure that the table is self-explanatory. All the “footnotes” included at the bottom of the table include important information to interpret the data and thus should be included in M&M (some of this info would help to answer some of the below questions). It would be helpful to provide statistical tests among periods and states, and rewrite the results of this subsection in light of the result of these statistical tests. This Table arises some issues on how the calculated variables should be interpreted. It would be nice to add some text in the M&M helping the reader to interpret these values. Another possibility is to focus on the mass balance calculations (now in the discussion). More specifically:

1. How can external CO2 sources be negative? This suggests that there is some other unaccounted process fixing CO2, and also uncertainties associated with your calculations, which should be better constrained. Overall is unrealistic to think that groundwater is not supplying, but consuming CO2.
2. How can be the contribution of internal processes to total CO2 evasion (i.e. -NEP/CO2) a negative value as reported for both the autotrophic-CO2 source? In this case, I would say that the contribution of internal processes to CO2 evasion is 0%, and that photoautotrophic organisms are contributing to fix more CO2 than supplied by groundwater.
3. How can the contribution of internal processes to total CO2 evasion be higher than 100% as reported for the autotrophic-CO2 sink state? In this case, are photoautotrophs fixing CO2 from the atmosphere to fulfill their photosynthetic requirements?.

L283. Better fully write down what -13%/12 years mean, since this is an important result. The same in line 289.

L292. Better write “with either annual discharge or annual temperature”.

L292. What about the other two states?

L276-281. So, if there is a 62% reduction in external inputs, but only a 13% reduction in discharge, what could explain the reduction in groundwater CO2 concentration over time?

Figure 3. Why did you use Theil-Sen slopes rather than regular linear slopes? Mention this briefly in M&M. Add “only for the heterotrophic-CO2 source state” in f.

L301. The M&M methods should better explain how the seasonality is imbedded in the rising and falling stages of the discharge.

L305- “and from CO2 sink to source”. Really? It seems the stream was acting as a source almost all year in Figure 4, except for some particular days.

L309. “The contribution of external sources largely mirrored these patterns” This sentence needs some extra clarification.

Figure 4. Why are you showing temperature in the color ramp?  

L316. Add “the” between “in” and “three”.

L317-328. Is this analysis of the hysteresis at 300 m3/s really a fundamental result of the paper? I understand the authors are doing this analysis to showcase the seasonal patterns exhibited by the variables studied. But this is already shown in Figure 4. My suggestion would be to withdraw these text (and Table) from the results and just select some of these numbers to illustrate the magnitude of these seasonal changes in the discussion.

L319. I don’t think the lack of slope makes the relationship more linear or more predictable than in the previous two decades.                               

Discussion

L330-342. In this first paragraph, it might be good to put some numbers to this “re-oligotrophication process”.

L336. How do the authors explain such a decrease in external CO2 sources? Is because decrease in groundwater discharge, CO2 concentrations, or both? This comes very late in the discussion, but may be good to provide some hint here.

L331. Add “contribution of” before “internal source”.

L340-342. The reason why the authors expected to observed a weaker discharge control on FCO2 when macrophytes dominated is not clear in the introduction, so it is difficult to follow the rationale here. Not clear either what the authors mean by “weakened discharge-external CO2 source”.

L347-349. Can you be more specific on how climate or environmental changes influence the occurrence of trophlux transitions?

L354. Be consistent with terminology throughout. Delete “metabolic”, the trophlux state does depend on the metabolic regime by definition (bis in line 356). Not clear what these ranges in parentheses are referring to, is this a range for the three decades? Perhaps it would be easier to provide an average value of the annual occurrence for the 32 years.

L359-363. Has this oligotrophication process being accompanied by changes in DOM? Why a decrease in nutrient availability has influenced GPP more than ER?

L370. Actually, more than a data point! You could say, for instance, “This study sheds new light” or “it’s a relevant contribution”….

L372. Not sure “rigorously” is the best adjective in this case, something like “quantify at high temporal resolution” may be more appropriate.

L379. “the temporal evolution of discharge is equally important to its magnitude”? Clarify, please.

L403. Change “had an annual CO2 sink” by “was acting as a CO2 sink”

L410. Why large river autotrophs benefit from being less affected by external CO2 sources?

L411. Well, if it occurred in 2005, it was not a “long-term shift”, but an “abrupt shift”.

L415. Provide in parenthesis the rate of annual increase in temperature and of decrease in discharge to get a sense of the magnitude of these changes without the need to dive on to the supplementary materials.

L417. Therefore…oligotrophication implies an improvement of water quality but a decrease in the capacity of the river to act as a CO2 sink. This seems like an important take home message.

L422. Which “linkage” and “the variation” of what? Do you mean, that a decrease in FCO2 over time cannot be attributed to changes in groundwater inputs because discharge showed no clear decreases over time?

L423-425. According to figure S7 and S8 discharge explains from 19-26% of external CO2 sources.

L439. “low frequency variation” of what?

L439-450. Overall, I found this part of the discussion quite speculative. Afterall, why groundwater CO2 fluxes have decreased so in the last decades? How the observed multi-annual low frequency variations relate with the results presented? How can these groundwater inputs be constrained in future studies?

L462-464. Not sure what the authors mean in this sentence. Could you rewrite?

L455-468. Could you be more specific about what do you mean with “new exploration” and “extrapolation on river networks”?

Figure S7. Mention the color ramp in the caption.

Figure S9. What means NGF? Check units for annual external CO2 (g C m-2 y-1)

General comments

Nguyen et al. report on long-term CO2 and metabolism data in a large temperate river. They show long-term shifts in the autotrophic/heterotrophic balance of the river, which they link to management changes that occurred since the early 2000s (i.e. lower nutrient inputs leading to lower GPP and a more heterotrophic river). Their data also suggest strong seasonal variations in both metabolism and CO2 emissions. Interestingly, while the river becomes more heterotrophic over time, hence with increased internal CO2 production, CO2 emissions tend to decrease in parallel. The authors attribute this decline in emissions to a decrease in external CO2 inputs at the catchment scale. They also show extreme year-to-year variability in both river metabolism and CO2 emissions, a finding that confirms the limitations of single-year studies and the need for long-term data where feasible.

This is a potentially great study based on a rare long-term dataset of paired O2 and (indirect) CO2 measurements. The study offers insights into the links between river metabolism and CO2 emissions, an emerging research area that is receiving some attention in smaller streams but remains unexplored in larger rivers – even less so over such extended timeframes. The findings should be of broad interest to the community, as improving our understanding of the temporal variations (diel, seasonal and interannual) in the source/sink status of rivers is a priority. However, several aspects of the paper require some improvement before it can be published.

First, the Methods section lacks details that can help readers assess the robustness of the datasets and the validity of the methods. I see some details are in the SI, but some information should appear in the main text. Details regarding any QAQC of the pH, alkalinity and oxygen datasets are crucial, as the entire study relies on these parameters. Importantly, the authors mention somewhere that older membrane sensors were replaced with optical sensors in 2008. This date coincides with a clear step increase in pH values and a resulting decrease in pCO2 values (as expected) and CO2 emissions (Figure 2), which brings up a crucial question: how much of the observed long-term decrease in CO2 emissions is a result of this sensor change? How confident are the authors about the continuity of the pH measurements across the entire time-series?

On another note, the metabolism modelling using streamMetabolizer is described too briefly, and there are no details on the conversion of metabolism fluxes (expressed in O2 units) into CO2 fluxes (unless I have missed it). The indirect estimation of k600 is another area that needs to be further scrutinised – where and when do the two methods (empirical models versus metabolism) yield the largest discrepancies, and why might that be?

Second, some of the interpretations, particularly regarding the potential drivers of the observed long-term decrease in CO2 emissions, need to be expanded. The authors mention a decrease in external CO2 sources, but could this trend instead reflect carbonate buffering processes, i.e. the conversion of some of the CO2 into alkalinity? As the authors do not seem to have collected any pCO2 data in shallow groundwater, could the above hypothesis be tested by updating their mass balance in Figure 5 with an additional term representing the downstream export of CO2 and/or DIC? Alternatively, have the authors considered any concomitant land use change that could explain some of the decline in CO2 inputs? Or could the decline be, at least in part, an artefact related to the sensor change in 2008?

On another note, I would invite the authors to discuss how representative their single measurement site is of the whole river system. Are the findings scalable to the entire river system? Some of the authors have worked on spatial variations in metabolism across river networks, so this should be a relatively easy addition.

Specific comments

Abstract

L30. Remove “was” in “the degree of which was depended”

Introduction

L37-38. This statement should be updated with the more recent estimates in Liu et al. (2022). https://www.pnas.org/doi/abs/10.1073/pnas.2106322119

L47-49. While I agree that seasonal and interannual variations remain under-studied, this statement omits recent studies that report paired CO2 and DO measurements for several years. Perhaps tone this statement down a bit.

L77. “most eutrophic river”

L86. “NEP decreased by approximately 10%”

Methods

L117-119. What sensors were used for pH and DO measurements? What was their measurement range, accuracy, frequency of cleaning and calibration? Some of this information is in the SI but much of it should be moved to the main text.

L121-122. What is the uncertainty of indirectly estimating alkalinity on pCO2 estimates?

L131-132. “To avoid unrealistic estimates of K600, values were constrained…”

L130-141. This section on metabolic modelling needs additional methodological details. Please specify the priors used in the model, how model performance was assessed, etc.

L153. Remove “the” before FCO2.

L156. Remove one of the occurrences of “with”

L157-159. It would help to show a scatter plot comparing the k600 values from the Raymond models with those from streamMetabolizer, so readers can see how well they match. Also, please explain why the two estimates might be different at high and low flow. As importantly, please clarify which quotients were used to convert O2 fluxes to CO2 fluxes, and explain how those values were chosen.

Results

L206. It would be useful to show (at least in the SI) a plot of the long-term DO time-series.

L210. “autotrophic/heterotrophic for NEP, sink/source for FCO2”

L236. “while there was”

L229. Figure 2. It seems that most of the decrease in pCO2 is driven by an increase in pH rather than a change in alkalinity. How confident are the authors that this is not related to the sensor replacement that occurred in 2008?

Discussion

L336-337. What explanations can the authors put forward to explain such decreases in external CO2 sources? Are they discharge-related? Do they relate to biogenic or geogenic sources? Can the decline be the result of carbonate buffering, i.e. some of the CO2 is converted to alkalinity follwoing increases in pH?

L374-377. Solano et al. (2023) present a figure summarising the range of percent contributions of NEP to FCO2 across the literature, which could provide useful context here.

https://aslopubs.onlinelibrary.wiley.com/doi/full/10.1002/lno.12334

L418. OK, some of my earlier questions are addressed in this section. I still think further discussion is needed, particularly regarding the potential influence of the sensor change in 2008, and the role of carbonate buffering. On this second point, I suggest integrating downstream export into the budgets presented in Figure 5.

L440. Add “scales” after multi-annual and decadal.