the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
| 10 Jun 2026
Towards a process-based estimation of global lake methane emissions using LAKE2.6
Abstract. While lakes play an important role in global methane (CH4) budget, the present meta-analysis based global estimates produce large uncertainties (16.5 to 185 Tg CH4 yr-1), which were often due to lacking sufficient geographical and spatio-temporal representations. Here, we applied a one-dimensional process-based CH4 emission model (LAKE2.6) to simulate global lake CH4 emissions. We first calibrated the model in 10 boreal and temperate lakes and 5 tropical (24 °S–24 °N) lakes with continuous flux observations spanning 2 months to 8 years, and subsequently proposed a novel parameterization scheme for global lake CH4 simulation based on these site-level calibrations. For global model validation, flux observations in 155 lakes from boreal and temperate regions and 21 lakes from tropical regions were collected, ranging in depth from 0.1 to 572 m and in size from 6 m2 to 67,075 km2. We found that simulated CH4 fluxes in 85 % of boreal and temperate lakes and 38 % of tropical lakes were consistent with observations, with relative biases within ±50 %. Based on these model calibration and validation results, we established a global parameterization framework and applied it to simulate global CH4 simulations. Our estimates show that global lakes (>10 ha) emitted 17.7–20.1 Tg CH4 yr-1 during the period 1979–2023. This approach improves the reliability of model extrapolations from site-level measurements to the global-scale, thus strengthening our ability to assess historical and future changes in global lake CH4 emissions.
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RC1: 'Comment on egusphere-2026-2349', Anonymous Referee #1, 06 Jul 2026
The authors applied the one-dimensional process-based CH₄ emission model LAKE2.6 to simulate global lake CH₄ emissions. They first calibrated the model using 10 boreal and temperate lakes and 5 tropical lakes, with continuous flux observations spanning from 2 months to 8 years. Based on these site-level calibrations, they proposed a new parameterization scheme for global lake CH₄ simulations. They then validated the model at the global scale using flux observations from 155 boreal and temperate lakes and 21 tropical lakes. Finally, they applied the calibrated and validated parameterization scheme to estimate CH₄ emissions from global lakes.Overall, the manuscript is well organized and clearly written. However, I have several major concerns that should be carefully addressed before publication.1. I am not fully convinced by the proposed parameterization of P0 and αnew, because the statistical relationships fitted in Figure 7 are based on only 10 lakes. It is highly challenging to upscale such relationships to more than one million lakes globally. I understand that the relationship between P0 and mean air temperature during the ice-free period may be reasonable to some extent, but there are likely important exceptions. For example, in lakes dominated by allochthonous carbon inputs from surrounding catchments, P0 may be more strongly controlled by carbon fluxes transported by streamflow, and precipitation or runoff may therefore be more relevant drivers than temperature. In addition, the authors included thermokarst lakes (shown in the global maps of results), where CH₄ production may be strongly controlled by permafrost thaw and the release of permafrost-derived organic carbon. In such systems, higher mean air temperature may lead to a longer thawing period and greater carbon availability for methanogenesis, which is a different mechanism from the general temperature–P0 relationship proposed here. Therefore, the current upscaling strategy for P0 may not be applicable to all global lakes.Similarly, although the relationship between αnew and the product of mean temperature and lake geometry may be statistically fitted, 10 data points are insufficient to support a robust global-scale parameterization. The authors should provide a clearer mechanistic explanation for this relationship. My concern is that these relationships are derived from calibrated parameters and may partly reflect numerical artifacts or parameter compensation rather than true ecological or biogeochemical controls. Do the authors have independent observations or parameters directly derived from measurements to support these relationships? For example, in Langenegger et al. (2019; https://doi.org/10.1002/lno.11133), similar parameters were derived from regression analysis based on laboratory measurements.2. LAKE2.0 is able to represent a valley-shaped lake geometry. I am wondering whether the simulations in this study used a valley-shaped or bucket-shaped lake configuration. If a bucket-shaped configuration was used, how did the authors distinguish CH₄ processes in pelagic and benthic zones? If a valley-shaped configuration was used, how were sediment CH₄ emissions distributed into different water layers along the sediment–water interface?3. The authors mention that LAKE2.6 simulates photosynthesis and respiration. More details should be provided on the parameterizations of these carbon-related processes, because they may be key controls on CH₄ production and emissions. Does the model explicitly simulate the growth of phytoplankton or macrophytes, especially rooted macrophytes with deep roots in lake sediments?4. The model was calibrated and validated mainly using datasets from Rosentreter et al. (2021), in which most sites are located in subarctic, boreal, and temperate regions of the Northern Hemisphere. However, in many subarctic and boreal lakes, allochthonous carbon inputs from surrounding catchments are important sources of substrate for CH₄ production. How are these external carbon inputs represented in the current model framework?5. I noticed that the authors included seven non-anthropogenic reservoirs in the model calibration and validation. What are the differences between the model settings for reservoirs and natural lakes when simulating CH₄ emissions?6. The authors state that the light extinction coefficient is an important parameter. For lakes without observations, empirical equations from Håkanson were used to estimate the light extinction coefficient based on lake depth. I agree with the general need for such an approximation, but the light extinction coefficient is also strongly related to inorganic suspended particulate matter, dissolved and particulate organic matter, nutrient status, and allochthonous carbon inputs. Therefore, using lake depth alone may introduce substantial biases in simulated thermal regimes and nutrient/light conditions. I suggest that the authors add a sensitivity test for this parameterization and explicitly discuss this limitation.7. Please add some explanation for the accumulated CH₄ emissions with increasing lake depth in Figure 3. The pattern for ebullition is intuitive, but the pattern for diffusive emissions is less clear. Why does the accumulated diffusive emission show this particular shape?8. In lines 333–334, the authors state that “LAKE2.6 could not simulate ebullition events with comparably high fluxes, which might be due to the uncertain mechanism of the pulse of CH₄ emissions.” I agree that gas bubble release can be stochastic to some extent, but the mechanistic distinction between diffusion and ebullition is relatively clear in process-based models, for example as described in Eqs. (16)–(17) of Maisonnier et al. (2025). The authors should explain how CH₄ production is partitioned between diffusive and ebullitive pathways in LAKE2.6, and why the model fails to reproduce high-flux ebullition events.9. In Section 4.1, too many numerical values are listed in the text for comparison purposes. A clearer approach would be to summarize the comparison between simulations and observations in a table, especially if the authors want to emphasize agreement in mean or total fluxes. Since many of these comparisons are already shown in figures, the text could also be simplified to avoid redundancy.10. Line 383: the authors state that they “hypothesized that a universal q10 value of 2.5 applies to all global lakes.” Was this hypothesis validated? If not, “assumed” would be more appropriate than “hypothesized.”11. I am confused by the parameterization of P0, which represents the CH₄ production rate. The authors state that LAKE2.6 simulates photosynthesis and respiration, which control carbon dynamics in lakes and the availability of substrates for CH₄ production. If so, why is P0 not directly linked to the simulated carbon dynamics within the lake?12. In Figure 8b, the comparison based on only four points seems to provide limited information and may not be meaningful.13. In Figure 10a, the horizontal axis indicates lake names rather than “observed.” Please revise the axis label and add a legend to distinguish observations and simulations.14. The model validation shown in Figure 10 seems to suggest that the proposed parameterization does not perform as well as expected. In particular, the results in panel a are difficult to accept unless the authors provide a convincing explanation.15. Readers may be interested in the computational cost of applying LAKE2.6 to global lake CH₄ simulations. Please add a sentence or short paragraph describing the computational requirements.16. Line 466: “hypothesized” should be changed to “assumed,” unless the hypothesis was explicitly tested.17. I am not sure whether LAKE2.6 is suitable for simulating CH₄ emissions from thermokarst lakes. Does the model include permafrost thaw and the release of permafrost-derived organic carbon? If not, the applicability of the model to thermokarst lakes should be discussed more carefully.18. Lines 485–490 are confusing. Do the authors mean that permafrost-affected lakes were excluded from the global analysis? If so, why do thermokarst lakes still appear in the figures? Please clarify whether thermokarst and permafrost-affected lakes were included or excluded, and how they were treated in the global simulations.Citation: https://doi.org/
10.5194/egusphere-2026-2349-RC1 -
RC2: 'Comment on egusphere-2026-2349', Anonymous Referee #2, 19 Oct 2026
Li et al. compiled a dataset of CH4 emissions from over 150 lakes globally to calibrate and validate the 1D process-based CH4 emission model LAKE2.6. They also developed a parameterization scheme to extrapolate site-level calibrated parameters to a global scale.
While identifying robust parameters for global lake CH4 simulations is a critical challenge in earth system modeling, I am ultimately unconvinced by the proposed methodology. The authors make several strong claims that are not adequately supported by the data or analyses provided. Furthermore, combining model development, validation, and global application in a single manuscript results in a scope that is overly broad, leaving individual components undertested. Given the major technical and conceptual concerns outlined below, I cannot recommend this manuscript for publication in its current form.
Major Concerns
First,I am not convinced that global lake thermal dynamics can be accurately simulated by calibrating only the light extinction coefficient. The light extinction coefficient primarily governs solar radiation attenuation within the water column; it does not account for other critical thermal processes such as sensible/latent heat fluxes, turbulent kinetic energy, or snow/ice formation and melting. Additionally, 1D models inherently struggle with the thermal dynamics of large or deep lakes, a limitation that a single calibrated parameter cannot resolve. Given the potential impact of this parameterization, a far more comprehensive validation of lake thermal profiles across diverse lake types is necessary.
Second, Calibrating only P0 and αnew is insufficient to represent CH4 dynamics across diverse aquatic environments, as these parameters govern production rather than oxidation or transport processes. It is particularly surprising that diffusive CH4 emissions were simulated without calibrating oxidation parameters, given that diffusive fluxes are highly sensitive to oxidation rates. Furthermore, the fraction of CH4 oxidized varies substantially across lakes, and Michaelis–Menten kinetics alone have been shown to be insufficient to capture this variability (e.g., doi:10.1007/s10533-019-00552-x).Third, I am not convinced that the parameterization scheme derived from only 10 lakes is generalizable to global lake environments. Figure 7a implies the existence of a negative correlation between air temperature and the quantity of biologically available OC in sediment, which has not been reported in any of publications. Because sediment OC relies on primary production and terrestrial OC inputs, based on Figure 7a, either primary production or terrestrial OC inputs or both need to negatively correlated to air temperature, which contradicts with many observations. Figure 7b lacks empirical support within the study's own framework, as evidenced by the authors manually overriding αnew to 11 m-1 for poorly performing lakes. Because αnew depends on complex sediment processes (OC deposition, mineralization, and sediment accumulation rates), its natural spatial variability is far greater than what can be captured by the limited calibration dataset.
Forth, permafrost-affected lakes were included in the global simulations despite being completely absent from the model calibration and validation datasets, making global emission estimates over high-latitude regions unreliable.Fifth, I find weak model-data agreement in the study. Given that the model was evaluated against observations at a monthly time step, the goodness-of-fit shown in Figures 4, 5, 6, 8, and 10 is inadequate, including 1) R2 values for several lakes fall below 0.1 (Figures 4–5); 2) observational data frequently fall outside the 5th–95th percentile confidence intervals of the simulations (Figures 8 and 10); 3) spurious model behavior goes largely unaddressed. For instance, Figure 4 exhibits unexpected double peaks in diffusion and ebullition across multiple years; Figure 5a–c shows radically different seasonal patterns for lakes under similar climate regimes; and Figure 6 shows a complete misalignment between observed and simulated monthly variability at Trout Bog.
Sixth, the spatial configuration scheme for global simulations relies on several untested assumptions: 1) merging lake areas within the same depth zone artificially inflates the area factor used to calculate αnew from Figure 7b, 2) representing the depth and area of each grid cell using median depth and logarithmic mean area was not evaluated to determine if it conserves total CH4 emissions relative to individual lake simulations.Other major comments:
L105–106: Clarify whether lake bathymetry is explicitly represented in LAKE2.6. If lakes are approximated as vertical cylinders, explain how CH4 emissions from littoral zones are accounted for.
L119–120: How can you verify that the sensitive parameters identified for specific test lakes remain the most sensitive parameters globally?
L134: Given that the model contains 15 parameters, 500 Monte Carlo iterations are unlikely to adequately sample the high-dimensional parameter space.
L135-136: Address whether the single lake selected for parameter sensitivity is representative of global lake diversity.
L164–165: Does this implementation imply that shallow lakes have extremely thin sediment layers? Please evaluate if this assumption is physically realistic.
L305–308: This implementation is also arbitrary.
L382: Explain why the q10 value from Gudasz et al. (2010) was not used directly if a universal temperature dependency factor was applied.
L404–405: Light attenuation cannot be reliably constrained by surface water temperature alone, as surface absorption represents only a fraction of the total surface heat budget.
L667: Clarify how the concentration of SO42- was set in the simulations.Other specific comments:
L83: Please explain why you only include lakes > 0.1 km2.
L206: Specify which seven lakes are being referred to here.
Figure 2a: Explain why the large tropical lakes used for calibration are omitted from the map.
L230: The dataset from Rosentreter et al. (2021) includes short-duration or sparse sampling events. Specify the filtering and preprocessing criteria applied to these observations.
L267: Clarify the relevance of ARC-Lake surface temperatures to validating CH4 sediment dynamics, given the thermal decoupling between surface waters and sediment. Additionally, clarify whether satellite ice-cover data were incorporated into the validation and if not explain the rational.
L294: The first and second parts of this sentence appear contradictory. Please rephrase for clarity.
L298: Provide empirical or literature support for the claim that the light attenuation coefficient is the dominant parameter governing thermal dynamics in tropical lakes.
Figure 4(j-i): Explain why no diffusive CH4 flux was simulated during 2009 for MH and IH.
Figure 6: Note that high-frequency eddy covariance CH4 flux data are available for Toolik Lake (e.g., Tan et al., 2024) and should be utilized for validation.
L381: Note that Walter and Heimann (2000) is not a lake sediment incubation study.
L483–484: Specify the spin-up duration and initial soil/sediment thermal and carbon pool states used prior to the production runs.Citation: https://doi.org/10.5194/egusphere-2026-2349-RC2
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