Särkelä et al. describe the carbon balance of the Siikaneva wetland from 2005 to 2021, focusing on the role of the non-growing season. They find that while this fen is in principle a sink for CO2, that it became a source in 2016 due to an unexpected large release of CO2 at the end of the cold season, and they attribute this to the release of CO2 built-up during the winter that remained trapped due to the frozen soil. I find this study well-written and focused, and the proposed mechanism for the large release of CO2 late in the cold season makes sense to me. I have a few suggestions for improvement, but most of them are minor.

My main concern is the use of the word growing and non-growing season, because I’m not sure that the term is correctly used here when using NEE as a threshold. For example, the authors mention that the non-growing season already started on July 30th back in 2018. However, this is a famously warm year with an extensive drought which of course stimulated ecosystem respiration. This is also clear from Figure S3. Did the plants really stop growing in the middle of summer, or did ecosystem respiration simply outweigh GPP? The authors refer to Körner et al. for their definition, but that paper suggests a different term when using NEE as a threshold: the productive season. This is of course an easy terminological fix, and I suggest using the productive season – or productive growing season if need be – to avoid confusion. The term non-growing season would have to be altered accordingly, because the same issue applies there.

Also, it would be good to see what the meteorological growing season would look like. For this, it would be very helpful if a figure similar to Figure 2 could be made that shows air temperature instead of NEE, which is much clearer than what’s shown in Figure S1. Similarly, it would be helpful to have such figures for GPP and Reco as well.

Otherwise, the event that occurred in early 2016 is very reminiscent of the conditions of a frost drought. This can lead to extensive shrub and tree damage. While the sedges, rushes and mosses present at Siikaneva are probably quite resilient to such events, it is possible that some vegetation got damaged and that this delayed the uptake of carbon after snowmelt. Was the onset of GPP later than in other years when comparing to, for example, growing degree days or a simple temperature sum?

Detailed remarks:

Line 68: “no-growing” should be “non-growing” (or non-productive)

Line 100: This looks like a sentence remnant that should be removed.

The manuscript by Särkelä et al analyses a 17-year eddy covariance CO2 flux dataset from a boreal fen to investigate the drivers of non-growing season CO2 fluxes. The authors present an interesting paper, use a unique, long-term dataset, and report novel findings. The research question is highly relevant since a better understanding of the non-growing season fluxes is needed to better understand interannual variability in carbon uptake and its response to climate change. However, in my opinion, the manuscript could be substantially improved if the following issues can be addressed.

1) One main working hypothesis and finding of the manuscript is that warm fall temperatures and a cold spell during mid-winter cause enhanced CO2 losses turning the fen from a CO2 sink to a source. First, I think the manuscript would benefit from a more detailed discussion of the underlying processes supporting this synthesis. Second, it remains unclear to me how the "release of the stored CO2 in the peat" can lead to an increase in emissions. If the freezing of the topsoil led to accumulation of CO2 in the peat column, then the resulting fluxes would be merely shifted. Mid-winter fluxes would be smaller and spring fluxes higher. For annual fluxes to be increased, respiration during the NGS must be higher, which could be driven by warmer soil temperatures. I think the distinction between CO2 production and transport should be discussed.

2) The authors mention that they partitioned NEE into GPP and Reco. However, they do not discuss the dynamics of the component fluxes and how they contribute to the 2016 event. While GPP and Reco are not directly measured, they can nevertheless help explain patterns in NEE. Furthermore, the differences in April/May might be, at least partially, be explained by decreased GPP. There is the possibility that the cold period with barely any snow cover caused frost damage leading to lower GPP in the spring. The cold event was very extreme compared to the other years. However, in the current manuscript, it is less discussed than the warm fall.

3) The authors provide a clear definition of the growing season and non-growing season. Their definition is identical with carbon uptake period. The authors could consider if the definition should rather be based on GPP, which is directly related to plant productivity, and thus a better indicator of growing conditions. Since NEE includes soil respiration, the authors' definition of GS may include periods of vegetation growth.

4) The NEE anomaly in 2016 was unfortunately preceded by a period of missing data. The authors address this and even detect differences in budgets when disregarding the period of missing data. However, if the CO2 emissions were shifted from mid-winter to spring, then the mid-winter period is crucial since emissions would be suppressed. Additionally, the gap-filling algorithm (which seems to be a photosynthesis and respiration model) might underperform due to the extreme conditions during this period, which are therefore not included in the model fitting. Could the authors assess the gap-filling performance shortly after the end of the data gap in 2016?

Additional comments:

line 18: Could the other provide the standard deviation for this estimate of 57%?

line 105: Why did the authors choose a 75% flux footprint. More commonly, 80% or 90% is used. Their definition leaves a quarter of the signal to originate from other surfaces.

line 111: Was the WPL term applied for a closed-path system? Why not calculating fluxes using mixing ratios?

line 115: It remains unclear what the length of the "period" is.

section 2.5: Please add citations to this section. What is the temporal resolution of the satellite data?

section 2.6: In my opinion, the random forest analysis only contributes little to the explanation of observed dynamics. The authors should consider providing more information on the model performance. Additionally, it seems as if they mostly focus on soil temperature as a driver. Would there be other simpler statistical analysis to investigate the relationship between soil temperature and lagged effects? Or could the three soil temperature aggregations be used in the same statistical model to test, which aggregation has the most predictive power? As it is presented now, it remains unclear how legacy effects and instantaneous affects are clearly separated.

line 180: Could there also be legacy effect from WTD?

line 215: Which test at which level was used here?

Fig. 4: October data is not shown. However, the authors discuss the October/November anomaly. Additionally, the delayed topsoil thawing could result in supressed GPP, which is not discussed.