Review of ‘Carbon emission and export from Ket River, western Siberia’ by Lim et al.

General comment

In this work, Lim and colleagues reported the spatial and seasonal dynamics of C export and emissions from the Ket River mainstem and major tributaries by combining continuous in-situ measurements and discrete sampling. Although high latitude regions are an important component of the global carbon cycle due to their large carbon stocks, carbon emissions and export from permafrost-affected regions, especially those in Russia, are poorly studied due to logical constraints and inaccessibility. In view of the changing climate and thawing permafrost, this study is timely important in quantitatively assessing the spatial and seasonal patterns of dissolved carbon export and emissions in this permafrost-affected river basin and thus provides important insights into future riverine carbon cycling. This research work fits well with the scope of the journal Biogeosciences. But there are several major issues to be properly addressed during the revision stage.

My first major comment is on the observed stable behavior of CO2 in the Ket River basin. The authors have tried to explain the stable behavior of the CO2 dynamics (pCO2 and Fco2) by relating them to various physiochemical parameters. But it seems none of the physiochemical parameters is sufficiently strong to drive the pattern although they show pronounced spatial and seasonal variations, as shown in Table 1 and Figs 2 and 3. This is contrary to studies in other climates/regions. I am wondering whether these potential drivers are working in different (opposing) directions and have counteracted each other. The authors may need to think about this seriously, and re-examine the cause-effect relationships. Many of the current discussion statements are lack of evidence and speculative.

My second major comment is on the calculation of the annual flux of CO2 emission and lateral C export. With very limited C sampling results covering a short period (Fig 1b), the annual flux estimates are prone to large errors. For example, CO2 emissions during ice melting periods are exceptionally strong after a long period of CO2 accumulation. But such emissions are not included or accounted for in the estimation. Likewise, the lateral fluxes based on monthly average discharge are likely with huge uncertainty. E.g., the strong DIC concentration differences between the flood and baseflow (Table 2) suggest significant dilution effect and changing flow paths.

Overall, this manuscript was well written, but the structure could be further improved by moving the discussion statements from the Results section to the Discussion section. A further language editing is also needed before its resubmission.

Specific comments (with line number):

L42-43: 100 to 150 times?  

L64: even for these regions, the estimates are still with great uncertainty.

L80: delete ‘remain’  

L95: essentially speaking, the two sampling campaigns represent the two extremes (highest flow and lowest flow, respectively). A question then is whether it is reasonable to use these extremes for annual flux estimation (emission and downstream export)?   

L108: what is hydrocarbon exploration? I don’t understand this.  

L113:  delete ‘.’ after -0.6.  also, references are needed to this paragraph describing the background information.

L119: Have the authors finished the cruise (1300 km in total) and sampling within 3 days? Sounds an impossible task.  

L125-126: what’s the sampling frequency for the day/night circle?  

L152: change ‘location’ to ‘locations’. Also, it would be helpful to briefly describe the measurement procedures, instead of referring readers to published papers for details. These papers might not be accessible to some of the journal readers.

L154: what are the standard approaches? Please clarify and provide details.  

L156: For flowing streams and rivers, the major driver of the gas transfer velocity is flow velocity, not wind speed.  

L181: The DIC concentrations in base flow is even higher than the DOC concentrations (table 1). But here the contribution of carbonate C to total C is only 0.3%. this looks problematic. please double check.  

L195: what is the spatial resolution of the biomass and soil OC content datasets?  

L219: a lack of systematic change? Note the pCO2 changed by a factor of 2 when tributaries with high CO2 concentrations join the mainstem.  

L241-247: these are not results, move them to the discussion section.  

L297-298: would the precipitation quickly infiltrate into soil and become groundwater?   

L306: as the measurements were performed at the flood peak, this may have caused overestimation.

L316: how were these %s determined?  

L338-340: why the co2 flux pattern is different from the pco2 pattern?  

L357-358: Another possible reason is because the measurements were actually not performed in the true headwater streams. All the sites, include the tributary ones, are located along the mainstem and not in the headwater region as shown in Fig. 1.   

L366-367: If allochthonous C inputs are the dominant source, pCO2 should have a clear relationship with distance to terrestrial C inputs, i.e., there should be higher pCO2 in tributaries than in the mainstem.

L402: change ‘at’ to ‘in’.

L427-452: For these comparisons (similarity and differences), it is quite difficult to follow. Putting them into a table may help. Also, the authors need to make a critical and comprehensive discussion, rather than a general sentence on the possible reasons. This is quite speculative.

L456: This ignorance may have caused great errors to the annual estimates. Emissions of CO2 during ice melting is exceptionally strong and make a disproportionate contribution to the annual flux estimate.

L460: unclear description of the Ob River.

L467: change ‘thus’ to ‘this’

L502-503: any evidence to support this argument?

Fig 2: for b&c, change the x-axis to 0-900 for consistency and easy understanding.

Fig 4e: much higher pco2 during the daytime than the nighttime? Why?

Fig 5d: very low r2, what is the p-value?

General comments

• The manuscript entitled “Carbon emissions from Ket River, western Siberia” provides a meaningful contribution to the understanding of carbon export and emissions in the western Siberian Lowland. The title of the manuscript is sufficiently precise and the overall presentation is well structured and clear. Many findings presented in this study are relevant and bring new insights into the processes and controls of carbon processing in this environment. Since the system is influenced by multiple factors, some of the interpretations raised in the discussion are relatively vague or inconclusive. Still, all interpretations and conclusions seem to be well supported by the results. For this reason, I believe that the manuscript will be suitable for publication in “Biogeosciences” after a careful revision.
• I applaud the initiative of using floating chambers for direct measurements. Although they require more work, the study would provide completely different and much less accurate FCO2 estimations if they weren’t employed. Maybe this finding could be emphasized in the abstract or in the final remarks.
• From a cost-effectiveness perspective, I do not see major problems in the approach you took for the final C emissions quantification (especially considering how difficult it is to perform multiple sampling cruises in these areas throughout the year). However, I think that the uncertainty calculation is too simplistic and most probably misleading. I urge the authors to follow best practices recommended at volume 1, chapter 3 of the “2006 IPCC Guidelines for National Greenhouse Gas Inventories” (IPCC, 2006). More specifically, Monte-Carlo approaches (based on probability density functions) have been successfully employed in other assessments. Also, the methods should show all the information required for reproducibility and traceability (e.g. by providing all the equations and later the full data set in online repositories). This does not seem to be the case in this manuscript.
• Estimations for lateral carbon fluxes and POC/DOC are not crucial for most of the conclusions in this paper and seem to be very simplistic and subject to large errors. I recommend authors to reconsider the importance given to the obtained values throughout the text and to improve methods section for a better traceability in this part.

Specific comments:

Lines 34-35 = Poorly known?

Lines 42-43 = Please consider also including the pCH4 ranges.

Lines 50-54 = Please consider revisiting these last sentences after a careful revision of the methods employed in the uncertainty calculations. I think it is important to be very clear on what are the limitations of these estimations right in the abstract to avoid poor usage of the emission values. For example, you mention in lines 50-51 that “C emission from the Ker River basin was estimated to 127+-11 Gg C y-1”, however, you’ve discarded important hot moments/spots, soil emissions/uptake, etc. I guess you should use another term instead of “River basin” here.

Lines 73-83 = please consider including some of the values instead of presenting this information in a more qualitative way.

Line 113 = I am not sure if “-0.6..-0.9°C” is a proper way of presenting the temperature range.

Line 201 = I am not a native English speaker, but “wetted streams” doesn’t seem right.

Line 226 = Please consider including the pCH4 ranges.

Line 244 = This may be a bit far-fetched, but what about emissions linked to vegetation or other hot spots that helps gas leakages? I know this is a completely different context, but something like seen in floodplain trees (e.g. Pangala et al., 2017), maybe? Also, some pictures of the river and streams in the supplementary material would help readers to have a better idea of the environment.

Lines 376-380 = To me it seems that you have raised a hypothesis (fluxes comes from bog water), tested it (calculate the bog area) and the results “falsified” your hypothesis. Shouldn’t you then present an alternative hypothesis here?

Lines 381-386 = Does it has any relationship with increased primary productivity per area inland? Any estimates?

Line 456 = Also mentioned “ket basin”, I guess this is inaccurate.

1) GENERAL COMMENTS

Lim et al. report a high-quality data-set of CO2 and CH4 concentration measurements in the Ket River in Siberia obtained during high-water and low-water. This is a very useful contribution to on-going efforts to collect data to better evaluate the carbon emissions from inland waters because the studied river drains a remote and nearly undisturbed (pristine) watershed dominated by peat bog and taiga forest. Unfortunately, the analysis is (in my opinion) not well structured and the authors might want to spend some extra time on thinking through how to present and analyze the data, and profoundly re-structure the paper and streamline the present content.

For instance, the authors computed the fluxes of CO2 with a gas transfer velocity parameterization for lakes; this gave (unsurprisingly) very different results from the fluxes of CO2 measured with floating chambers. This was predictable and in my opinion not very useful, just distracting. Regarding formal aspects, the authors should spend some extra time producing high quality figures. Figure 2 is extremely confusing and does a very poor job at presenting this data-set that required a lot of effort to acquire. Figure 3 shows some nice patterns of pCO2 and CH4 concentration in terms of seasonal variations (high-water vs low-water) as well as in terms of stream size (main-stem vs tributaries). A more straightforward and attractive presentation and discussion could be built on these simple patterns. Instead, this nice and potentially interesting information is diluted in a lot of rather unnecessary elements such as computations of fluxes with inadequate gas transfer parameterizations and correlations with not very useful variables such as total bacterial counts (see comments below).

2) MAIN COMMENTS

L37 and L218: I’m unsure that the term “continuous” applies to measurements of CO2 to this study. My perception of “continuous measurements” is that water is continuously pumped through an equilibrator system connected to a CO2 detector (or equivalent setup) and then the data are logged at regular intervals (1 min or less) (Abril et al. 2014; Crawford et al. 2016b; 2017 Borges et al. 2019). This means that the measurement of CO2 is not interrupted for long periods (and runs for a few hours to a few days) while the boat is sailing. The authors made discrete samples with the boat stopped at a given spot. Albeit they made numerous measurements this should qualify as discrete sampling and not continuous. This is not just a semantic issue; the authors made 764 pCO2 measurements over the distance of the boat route (834 km) as stated L 218. This roughly corresponds to one measurement every 1 km. This is still quite coarse to describe extremely dynamic river systems. As an example, Borges et al. (2019) showed very marked cross-channel gradients of CO2 in the mainstem Congo River, corresponding to a spatial scale of the order of 1 km (using what truly qualifies as “continuous”).

L150: The authors measured CO2 fluxes between water and air with floating chambers. Lorke et al. (2015) have shown that anchored chambers enhance turbulence under the chambers and artificially enhance fluxes, thus providing erroneous estimates. Please specify if the chambers used in the present study were anchored or free-drifting. If the chambers were anchored then the data should used with extreme caution, especially for the flood period when presumably the flow was higher. In my opinion, these chamber measurements are not necessary, and fluxes should be computed from gas transfer velocity using an adequate parametrizations applied to spatial data, please refer to Liu et al. (2022).

L154: The authors also computed the CO2 fluxes between water and air from CO2 concentrations and the gas transfer velocity. The cited references (Guérin, et al., 2007; Wanninkhof, 1992; Cole and Caraco, 1998) provide parameterizations for lakes that are inadequate for computing the gas transfer velocity in running waters. The authors provides these 3 references, although it was unclear to me which one was actually used in the computations. The gas transfer velocity in streams and rivers can be derived from stream flow and stream slope, that in turn can be derived from spatial data; please refer to Liu et al. (2022).

L 216: The authors state that there are no spatial variations in CO2. I suggest to mention here that CO2 in tributaries was higher than in the main stem. This corresponds to a “systematic” pattern of variation. Also, I suggest that the authors extract the Strahler order of the sampled streams and rivers and analyze if there are differences by stream size. It is quite frequent that lower order streams show higher CO2 values and higher order (Butman and Raymond 2011; Borges et al. 2019), although not always necessarily the case (Borges et al. 2018). Stream size could also be analyzed in terms of catchment area, in addition to Strahler order. Stream size can be used also for upscaling concentrations and fluxes, refer for example to Borges et al. (2019).

3) SPECIFIC COMMENTS

L 34 : I suggest to define « medium–size rivers »

L 34 : I suggest to remove « poorly » or replace by « largely » but « poorly unknown » is ackward.

L 40: I suggest to mention the months-years of sampling

L40: I suggest to replace “CO2 concentration” by partial pressure of CO2.

L40-41: I suggest to mention the differences in pCO2 between base flow and flood period.

L41-43: I suggest to provide the range of the CH4 concentrations values rather than the ratio to CO2.

L 47 : I suggest to specify if this is this spatial or temporal “variability” ? or both ?

L 49 : The hypothesis of lower path soil-water CO2 inputs during summer is based on what ? During summer-time numerous processes contribute to increase CO2 in rivers compared winter such as higher temperature stimulating microbial metabolism, longer residence time and lower gas transfer velocity (lower river flow), in addition to changes in flow paths of soil-water flows (Borges et al. 2018).

L51: “lateral” usually refers to exchange between river and riparian zones (e.g. floodplains). Term “downstream C export” might be more adequate. I suggest to specify if this downstream C export refers to inorganic, organic or total carbon and if dissolved or dissolved+particulate.

L67: define abbreviation pCO2

L69: This statement does not reflect current state of CO2 studies in rivers. There is a fast growing very large amount of studies reporting directly measured CO2 measurements either discretely (Alin et al. 2011; Borges et al. 2015; Amaral et al. 2018; 2022; Leng et al. 2022), continuously at fixed sites (Crawford et al. 2016a, Schneider et al. 2020; Gómez-Gener et al. 2021), and continuously underway (Abril et al. 2014; Crawford et al. 2016b; 2017; Borges et al. 2019). And this is also the case for studies in “under-represented or ignored regions” as stated, and for more than a decade (Alin et al. 2011).

L 71-72: This is correct and there are some studies available (Abril et al. 2014; Crawford et al. 2016b; 2017 Borges et al. 2019). It could be useful to briefly mention if there is and what is the added value to make continuous “regional high spatial resolution measurements” of CO2 compared to discrete measurements, based on past published papers.

L73-74: Please clarify what do you mean by “High latitude regions are important”. With respect to total CO2 emissions at global scale, rivers in high latitude regions are not important according to the study of Liu et al. (2022) who show that “tropical rivers are responsible for 57% of the global emission, more than temperate and Arctic regions combined (30 and 13%, respectively)”.

L113: there’s some sort of typo here “ 0.6..-0.9 °C”

L 148 : For a journal such as Biogeosciences I think it is insufficient to refer to other papers for basic methodological information. I suggest to provide details on the gas used for the headspace, on the calibration gases, on the detection limit, precision and accuracy. It could also be useful to mention the typical time interval between sampling and analysis.

L129-139: Similarly for CO2 please provide information on precision. Is the stated accuracy given by the manufacturer or was this determined by the authors? Also specify how the Vaisala instrument was calibrated. Did you trust the factory calibration or did you carry out calibration in the lab? Was the probe checked for signal drift before and after the cruise against standards ? Did you measure atmospheric CO2 with the Vaisala probe during the cruises as a check of good functioning ?

L 144 : how was the water sampled and transferred to the serum vials ? With some sort of sampling bottle ? Niskin or equivalent ?

L165: I suggest to define the “NIST” abbreviation

L189-193: Please specify if the land cover data correspond to the whole catchment area upstream of the sampling point or if this corresponds to the riparian vegetation just adjacent to the sampling point.

L 216 : I suggest to remove word « emission ». You cannot pre-suppose an emission, some rivers on some occasions can be sinks of CO2 (Crawford et al. 2016b).

L 246: I’m not sure this “warning” is useful since the authors used a parameterization for lakes, and this was not a very good idea to start with.

L 295 : It’s quite unusual to look into the effect of catchement lithology on fluvial CO2 and CH4 concentrations. Lithology will affect the HCO3- content and DIC content, but with little direct impact on CO2 levels and certainly not on CH4. I suggest the authors restrict this analysis to DIC (or remove altogether this analysis that is just a distraction).

L297-298: This is also quite unusual. I would envisage seasonal variations precipitation to explain seasonal variations of CO2, but not spatial variations during a given period, in this case base flow. Correlation does not necessary imply causation, some correlations are spurious or indirect. There’s a possibility that this is relate to stream size, as precipitation at catchment scale, also captures catchment surface area in an area of relatively homogeneous precipitation. I suggest to remove altogether this analysis that is just a distraction.

L 346: The paper of Gómez-Gener et al. (2021) gives a reasonably good account of diel variations of pCO2 in temperate rivers but reports measurement in an extremely limited number of sites in tropical rivers. So this study does not allow to make generalizations on “tropical rivers”. There are other studies in tropical rivers that have shown that diel variations of CO2 are undetectable such as the Congo (Borges et al. 2019) because aquatic pelagic primary production is low (Descy et al. 2018) due to strong light attenuation the water column by DOM.

L363-367: This is a reasonable explanation. However, “homogeneous landscape” and “strong allochthonous sources of organic carbon” can still lead to variations of CO2 per stream size, with small systems showing higher values than large systems as predicted conceptually (Hotchkiss et al. 2015) and verified at basin-scale (e.g. Borges et al. 2019).

L 381: I suggest to remove the word “interesting”. This is self-evaluation, let the readers decide what’s interesting. Same applies to word “notable” L 361.

L 477-515: Section “Concluding remarks” provides a summary of the paper and thus duplicates the content of abstract. This section could be removed or streamlined.

In Figure 2, I suggest to show the « continuous » pCO2 measurements data points as a discrete symbols (dots) rather than a line.

Figure 2 is incredibly confusing and in my opinion undermines the large sampling effort. I suggest to make separate figures for pCO2 and FCO2 and not try to show all of the data together in single plot. Please provide a graphical representation of the pCO2 during the flood period. If I understand correctly the symbols, the blue diamonds in plot A) are for the FCO2 and not pCO2 in the tributaries. But Table 1 shows that pCO2 was measured in the tributaries during the flood period. I also suggest to remove the “continuous FCO2”. The term is misleading since it’s FCO2 computed from “continuous” pCO2. Also since the figure mixes FCO2 measured with the chambers and computed with a gas transfer velocity and that the values are very different, the impression given by the figure is very confusing.

Figure 5 : pCO2 should be in the Y-axis and the potential predictors/descriptors (SUVA, land cover) in the X-axis.

The correlation of pCO2 and TBC in Fig. 5B is weak and not very informative. The TBC only informs on the presence of microbes and not their activity. Also, if CO2 comes from soil-water as suggested by the authors then it is not produced in-stream and we should not expect a correlation with TBC. This cannot go both ways.

4) REFERENCES

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