General remarks

The manuscript reports results from a) ca. 1.5 year continuous measurements of limnophysical and meteorological data and b) GHG data from 2 short and intensive summer campaigns in two Canadian thermokarst lakes. From these data the authors try to figure out how GHG emissions in the two lakes were regulated and come up with seasonal GHG budgets for the two lakes.

The topic of the study is important and interesting. GHG emissions from thermokarst lakes are relevant and not well studied. This is probably partly due to the logistic challenges connected with the topic. This makes the presented data very valuable. I appreciate the amount and quality of the dataset obtained under challenging logistic constraints.

However, I have 2 major concerns with the manuscript:

• In their third hypothesis they state that the study was conducted to estimate seasonal variability. However, the method approach is not suited to address seasonal variability of GHGs. Only measuring GHG concentrations and fluxes during two short summer campaigns does not allow to study seasonal dynamics. The authors try to circumvent the lack of seasonal GHG data by a clever combination of assumptions and limnophysical data. This is feasible, but cannot be a core element of the paper. Seasonal conclusions are not sufficiently supported by data. I recommend to adjust the aim of the paper and tone down the seasonal part of the paper accordingly. I recommend to focus more on the strong aspects of the paper: The combination of limnophyscial, meteorological and GHG data during the campaigns as well was the seasonal pattern of stratification and oxygen.
• The manuscript is rather long. This is partly because there are several redundancies between text and figures and tables (e.g. l.443, l.449) and also redundancy between discussion and results (see below). Also, the discussion is in large parts a repetition of the results and does not contain much new information. This is particularly true for section 4.1.. Also l.581-584 or l.590.

A strength of the dataset is that you not only calculated but also measured k600 (what not many people do). You hide in the supplement that both methods agreed fairly well. I recommend to exploit this more in the manuscript. Another chance you missed is: You quantified fluxes from k and concentration. Thus, you can exactly quantify the role of k versus concentration for flux dynamics (and not just write “likely” as in line 593 or “suggest” in l.629). See e.g. https://aslopubs.onlinelibrary.wiley.com/doi/10.1002/lno.12528.

Detailed remarks:

l.13: It’s a bit confusing that a colder summer had temperatures above long term average. Isn´t it more a hot versus a warm summer?

l.52.: “… ebullitive CH4 fluxes…”

l.120: They were not permanently anoxic in the bottom water. Maybe change to “with frequent anoxic conditions”

l.125: I doubt that Secchi depth can be measured at 1 cm precision. Remove “very”.

l.202: “Did you really deploy only one bubble trap per lake? As it becomes clear later in line 666 they indeed only deployed one trap. This is in my eyes not enough to come up with a robust estimate of ebullition.

l.215.: How were the exetainers vacuumed?

l.223.: It is not very common to use a (not very sensitive) TCD for this kind of study. This limits the precision of the concentration data. Please report detection limits and analytical precision for dissolved gas concentrations – not only ppm results.

l.225: Was the CO₂ change during the chamber measurements linear? 30 min is a rather long time for these measurements. Can you prove that linear fitting is not under-estimating fluxes?

l.227: Was the inner volume of the analyzer and the tubes involved?

l.242: Maybe add position of the traps to figure 1.

l.247: A partial pressure is not dimensionless but has a pressure unit. What you probably mean is “volumetric mixing ratio [ppmv]”?

l.249: How was the molar volume obtained?

l.300…: use past tense for results.

l.334: I do not see a data gap in the figure.

l.375: It is not very clear what “vertical structure” means. Maybe “vertical structure of the water column”?

l.376-77: Remove sentence.

l.392: Reformulate “While surface remained similar”.

l.393: Can you calculate how the density effect of the conductivity change compare to the temperature induced density?

l.396: What do you mean by “tilting”? Tilting of the thermocline?

l.426: Change to “atmospheric equilibrium values”.

l.454: Why only “likely”. You quantified k, so you should know.

L458: Please report bubble CH₄ content data.

Table 4 is redundant to Figure 7. The table can be removed to the supplement.

l.479: It looks as if concentrations were lowest 3 h after sunrise. Any explanation for this lag?

l.486: Why should concentration change when temperature changes. If you express concentration as %sat then yes. But absolute concentrations not. Maybe it makes more sense to use absolute concentration rather than saturation in Figure 8?

l.496: How was the standard deviation calculated?

Figure: Would be nice to have lines with wind speed or k in the plots.

l.560: is “heightend” the right wording?

l.595: How can this be done? Sample more lakes? Sample more site within a lake?

l.614: The temperature data are redundant and not needed here.

l.622: There are several other studies reporting diurnal pattern (e.g Golub, M., et al. (2023). "Diel, Seasonal, and Inter-annual variation in carbon dioxide effluxes from lakes and reservoirs." Environmental Research Letters and references therein)

l.647-649: This is not really a new conclusion. Maybe focus more on the special case of thermokarst lakes in the sense “not only in eutrophic warm lakes with a lot of biology but also in this peculiar thermokarst lakes diurnality needs to be considered”. Another interesting aspect of diurnality in high latitudes could be that (different to “normal” settings) there are periods without darkness in summer.

l.661: See also https://bg.copernicus.org/articles/22/1697/2025/ and

Table S2: Why not add the chamber flux data to this table?

Review of “Temporal patterns of greenhouse gas emissions from two small thermokarst lakes in Nunavik, Canada”

Here, Pouliot et al. conducted an intensive study on GHG emissions in two thermokarst lakes located within the same ecosystem but exhibiting contrasting limnological characteristics. The study primarily aims to synthesize data from two consecutive summer sampling campaigns, its main strength lies in the high-resolution diel and summer temporal sampling of GHG gases, as well several associated biophysical and environmental parameters. However, I recommend moderating the strong extrapolations made from these limited summer datasets to broader seasonal year dynamics. The study would be more robust if it is focused on summer observations and cautiously discussed the potential implications for winter and turnover periods before and after ice cover. I would argue that such extrapolation is quite vague, given that the diel patterns differ between the two sampling days across different years, even in subsequent day measurements in same ecosystem (Figure 5), data varies importantly. Therefore, your statement remains unclear whether these differences are due to actual environmental changes or simply the result of capturing a single day per year, which may not adequately represent diel or yearly variability. Below see other comments about the manuscript that would help you to improve it.

Please work on improving the methodology section as it is currently difficult to follow. Consider moving some detailed information to the appendix or supplementary materials, while expanding explanation of key topics. A comprehensive data table would help clarify your sampling approach. For example, it is unclear how many samples were collected for the diel analysis, subsequent days GHG measurements during the summer campaigns, and other parameters. I said this because, I cannot determine the source of the N values reported in Tables 3 and 4 or whether they come from the diel sampling. Besides, consider consolidating related tables (e.g., Tables 1 and 2 could be merged).

Regarding buoyancy frequency calculations, please clarify how you determined water density in the ponds. Did you incorporate your measurements or use arbitrary values? This section needs a more detailed explanation.

The CH4 ebullition methodology requires expansion, particularly since it represented the primary CH4 source to the atmosphere in one pond. Please explain the bubble trap attachment system that prevented movement during the 11-day deployment. Additionally, specify the number of bubble traps used and their spatial distribution across the lake. The issue arises because small replicate ebullition traps may not fully capture ebullition events, Wik et al. (2016, doi: 10.1002/2015GL066501) provided important insights on this topic. Therefore, the argument based on Figure S5 is not valid, the images do not clearly show ebullition, and any observed bubbling could be due to other gases, such as oxygen produced by photosynthesis. If the bubbles were indeed methane, the corresponding diffusive fluxes and surface concentration would be extremely high, which is not supported by your data. Please acknowledge that your dataset is biased, as you mentioned, but avoid overinterpreting the results with vague or unsupported statements.

Regarding the CH4 and N2O measurements, I was quite surprised by the reported sensitivity of the GC-TCD, especially its ability to detect concentrations close to atmospheric levels for CH4 and even lower for N2O. Are you certain that a TCD was used for these analyses? If so, I strongly recommend that you provide more detailed information on the calibration procedure, the sample injection volume, and the type of column used. This would be highly valuable for researchers working with similar GC-TCD systems. I am particularly skeptical that N2O concentrations below atmospheric levels can be reliably detected using a TCD. However, if this is indeed the case, please elaborate on the protocols that enabled such sensitivity.