The manuscript by Zhu et al. examines the net ecosystem CO₂ exchange over a subalpine coniferous forest on the southern margin of the Qinghai-Tibet Plateau (QTP) from 2020 to 2022, using the Eddy Covariance technique. They found that the subalpine coniferous forest acted as a net carbon sink during the two years of EC observations, with an average annual NEE of -389.03 g C m^-2. Additionally, they synthesized NEE data from 49 other EC sites covering most of the ecosystems in the QTP and concluded that NEE is negatively correlated with elevation. This study has the potential to provide valuable baseline information on CO₂ fluxes from the understudied QTP subalpine coniferous forests and enhance our understanding of the global carbon cycle. The research methods are innovative, and the results are significant to the carbon cycle research community. However, the following concerns need to be addressed in the revision before this manuscript can be considered for publication in the journal Biogeosciences.

1. Some extra data quality control on the eddy covariance (EC) measurements is still needed, and much key information was still missing. Firstly, in lines 180-184, it is not clear for me how the authors discard nighttime NEE data that were observed when friction velocity (u*) is less than 0.28 and 0.39 m s^-1. More importantly, there is no such u* criteria of 0.28 and 0.39 m s^-1 in the study of Papale et al., 2006. Besides, based on my understanding in Eddy Covariance data processing, the “0-1-2” labels (which were mistakenly interpreted as a method to evaluate the turbulence steadiness, in line 177) are not enough for the quality control, extra steps such as the median of absolute deviation about the median (MAD) method from Papale et al., 2006 should be applied to detect the outliers as well. In addition, the number of measurements that were discarded in each outlier detection should be revealed in order to evaluate the quality of the EC dataset. Secondly, the footprint analysis results should be stated in the manuscript. At this stage, key information about the underlying terrain, the composition of each tree species in the forest, the age of the forest, and the footprint of the EC tower are still missing. Finally, in Lines 188-189, it could be problematic to set the storage flux as zero. Since continuous concentration profile measurements are lacking in this study, I suggest the authors apply the decoupling filtering method (Thomas, C.K., Martin, J.G., Law, B.E., Davis, K., 2013. Toward biologically meaningful net carbon exchange estimates for tall, dense canopies: multi-level eddy covariance observations and canopy coupling regimes in a mature Douglas-fir forest in Oregon. Agric. For. Meteorol. 173, 14–27.) to account for both the storage and advection effects.
2. The introduction and discussion part seem to me a bit plain. Both the importance of subalpine forests in the QTP and its correlations with climate change factors in regard to NEE, GPP, and ER are not deeply revealed and discussed. I recommend the authors to elaborate more on the degradation of permafrost in the QTP and the coming upward migration of tree line. In addition, only linear regression was used to explain the links between NEE and environmental factors. It is highly recommended that the authors utilizing other advanced methods such as PCA loading or wavelet analysis to reveal the details in these correlations.
3. The division of seasons is ambiguous to me. In Lines 18-19, the authors used the term growing and dormant season. However, the length of the growing season and dormant season is missing, making it hard to follow what the authors are trying to describe. As for the normal four seasons, I assume the authors used the common calendar which delineates them into three months each season. This might be not useful for evaluating the seasonality of NEE since the vegetation status was not illustrated. I would suggest the authors carefully define the length of growing and dormant seasons based on relevant conditions such as air temperature and soil moisture and then analyze the seasonality of NEE and its climatic controls.
4. The comparison of NEE measurements from ecosystems over the QTP seems redundant to me. Even if the compilation is needed for this study, details such as the number of each ecosystem, the year of the observation, and the general environmental factors (air temperature, precipitation) should be illustrated clearly. It is also important to explain how the average NEE of each ecosystem was calculated and how these sites can represent the same kind.
5. Line 29, the NEE value should be negative.
6. Line 30, rephrase the word “enormous” if you can’t support the argument with statistics.
7. Lines 39-40, references are needed to show where this number of 419 comes from and which year was the measurement.
8. Lines 67-68, this statement seems too arbitrary and could be controversial.
9. Lines 80-89, the description and review here seem too simple and redundant to me.
10. Line 133, delete this sentence.
11. Lines 134-135, add relevant references to show where these measurements come from.
12. Line 139, be careful when using the term “vegetation resources”, would be better to be more specific.
13. Lines 141-144, refine these sentences to focus more on the subalpine forest ecosystem.
14. Line 147, the source of the ecosystem type map needs to be reported as well.
15. Line 152, it is the frequency of measurements rather than the response frequency.
16. Line 153, the specific heights need to be revealed here.
17. Lines 159-168, these basic eddy covariance descriptions should be more concise.
18. Line 169, should be calibration rather than correction.
19. Line 170, please confirm whether EddyPro has the function of outlier detection.
20. Lines 175-176, please elaborate on how this process was applied to the correction.
21. Lines 190-191, this is the gap-filling strategy, not filling the missing value.
22. Line 199, replace “a” with “α”.
23. Line 201, ecosystem respiration.
24. Line 2017-210, are both daytime and nighttime data gaps being filled using the Tovi software? The number of the gaps should be stated.
25. Line 211, we normally use the term “flux partitioning”, not “flux splitting”.
26. Line 222, what are the environmental conditions?
27. Lines 236-238, delete this sentence.
28. Line 241, what is 'short periods'? Please be precise.
29. In figure 2, the unit of VPD should be hPa rather than Pa.
30. Line 250, where is this nearby station, and which data was interpolated?
31. Line 255 and Line 258, the UTC+8 time needed to be revealed in the first place.
32. Line 258, the term “carbon sequestration period” is not defined.
33. Lines 261-265, rephrase this sentence.
34. Line 265, only one unit is required in this sentence.
35. Lines 270-271, the P value is not enough to determine the significance.
36. Line 276-277, delete this sentence.
37. In figure 4, please confirm whether the unit of VPD is correct or not.
38. Line 281, Figure 4. Relationship…
39. Line 283, delete “rate”.
40. Lines 313-318, more discussion and description are needed to support your claim of the “findings”. This writing style fits the conclusion part, not the result part.
41. Line 350, what is “ecological respiration sensitivity”?
42. Lines 386-388, more evidence is needed to support this conclusion.
43. Line 412, please confirm whether this reference style here is correct or not.
44. It would be better if the authors could show the standard deviation error bars in figure 3.

Zhu and others study carbon flux in a subalpine forest on the Qinghai-Tibet Plateau. The interesting findings weren't discussed and the manuscript did little to inform readers about how carbon exchange in this system works. Rather, values were mostly compared against other studies, which was at times interesting, and many statements about global change that were not of particular reference to this study were made, which was distracting. The study, especially the Discussion needs to be comprehensively re-written to focus on the interesting findings of the study rather than a wandering review.

line 20 is both remarkably general ('autumn') and specific ('12:30'). reporting extremes is tricky because it may be an outlier; I would simply exclude this passage.

23: it's already known that PAR is the most important variable if water or other factors aren't limiting. Can you say for certain that elevation is really the driver of carbon cycling or is it the climate characteristics that covary with elevation?

line 29 and elsewhere: I have no idea where or when it was decided that eddy covariance measurements are accurate to 5 significant digits. '389' or perhaps better yet '390' is more realistic.

how was the statement on line 32 determined?

40: simply also note the year and location (assumably Mauna Loa)

line 51-53: probably unnecessary to note in a study about forests in China.

line 67 is inconsistent with a study that uses eddy covariance to measure carbon dioxide uptake.

line 90 is confusing because this paper doesn't quantify feedbacks (which is hard to do). Simply removing it is probably best.

133: there is no typical mountain climate.

would the density of air not be needed for equation 1?

188: a storage flux of zero is not a safe assumption for a forest

190: this isn't exactly the Michaelis-Menten model; rather it's a rectangular hyperbola, which has the same shape (if the vmax and Km parameters happen to be identical)

2.4: this section is usually called 'flux partitioning' or similar.

3.1 can be shortened considerably. There's too much unimportant text. Remove all unnecessary words and does a reader really need to know the maximum and minimum of things like RH?

245: this is qualitative; anything over the light saturation point is 'favorable for photosynthesis'

257: I struggle to see how Beijing time is relevant for a study in southwestern China. Using the solar zenith angle is probably more useful in this section. I don't see any evidence from the figures that there's much of an afternoon drawdown; honestly this section mostly just says that carbon uptake follows light, which is already known. I recommend removing or dramatically simplifying.

Figure 4 requires an analysis of hysteresis, which would probably yield some interesting results. regression lines are not particularly useful here. Surprised to see that equation 3 wasn't used to study the response to PAR and that a linear model was used instead.

Statements like 'The forest ecosystem respiration rate was lowest in  winter and slightly higher in spring' are too obvious to really warrant mentioning, but differences in respiration between summer and autumn in different years are more interesting. The results section needs to be rewritten to focus on novelty.

297 and elsewhere: just remove everything to the right of the decimal places here.

section 3.6 was a surprise; previous text did not suggest that a synthesis would take place.

Figure 7 isn't really carbon sequestration potential. It's observed C flux. fewer significant digits and units are necessary.

323-335 is too well known to warrant mentioning. What is it that is unique about the present study system? everyone knows that plants need light and proper temperatures. VPD is based on TA and RH. It is interesting to note how the study system was constrained by VPD.

337: this study isn't about fires and logging. Everything from 335 to 350 is expository material. It doesn't belong in the Discussion, and was a random assortment of references that was not organized very well.

353: a discussion about why would be more interesting. Monson et al. (2006, GCB) and similar references covered this topic.

remove lines 371-378.

I absolutely cannot believe that the causes for differences in respiration in summer and autumn during different years was not discussed in the Discussion section, which is largely a poorly-organized narrative about different scientific studies.