the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
| 08 May 2026
Sensitivity of CO2 exchange in WRF-VPRM to model resolution and parameter settings over Alpine topography
Abstract. As the terrestrial carbon sink remains the most uncertain component of the global CO2 budget, systematic misrepresentation of biospheric CO2 exchange in complex mountainous regions limits the reliability of climate projections. This study employs the Vegetation Photosynthesis and Respiration Model coupled to the Weather Research and Forecasting model (WRF-VPRM) in real-case simulations over the European Alps. It investigates whether Alpine CO2 exchange is appropriately represented when using default or regionally optimized VPRM parameters, quantifies the sensitivity of modelled CO2 exchange to horizontal grid spacing at scales typical for global weather prediction (9 km) and climate models (54 km), and identifies the physical drivers of resolution-induced biases. Simulations with coarser horizontal grid spacing are compared with a regional-scale 1 km reference. Throughout 2012, 12 clear-sky and 12 cloudy/rainy days are simulated using three different VPRM parameter sets: default European (DF), Alpine-optimized (ALPS), and site-specific (SITE).
Validation against five Alpine FLUXNET sites indicates that the SITE parameters perform best overall. The ALPS configuration provides a nearly unbiased representation of ecosystem respiration (Reco) but overestimates gross primary production (GPP), whereas the DF configuration strongly underestimates both Reco and GPP. In DF, these biases partially compensate, resulting in comparatively good performance for net ecosystem exchange (NEE) despite physically inconsistent flux components.
Systematic biases in CO2 uptake and their magnitude depend on grid spacing and prevailing meteorological conditions. Resolution-induced biases in NEE (relative to 1 km simulations) under clear-sky conditions decrease from several percent (7 % for ALPS, 4 % for DF) at 9 km to near zero at 54 km. For clear sky, coarser resolutions yield higher net CO2 uptake. In contrast, under cloudy and rainy conditions coarse grids have lower simulated uptake than at 1 km, while the biases substantially increase (from order 10 % at 9 km grid spacing to over 40 % at 54 km). If yearly NEE is estimated from 12 days each for clear-sky and cloudy/rainy conditions, differences due to resolution are minimal at 9 km , while differences due to the parameter set (ALPS vs. DF) amount to 15 %. At 54 km grid spacing, resolution effects for both ALPS (17 %) and DF (13 %) exceed parameter effects (8 %). Taken together, the results imply that resolution-induced errors govern annual NEE uncertainty at coarse resolution (O(100 km)), but at finer resolutions (O(10 km)) the relative impact of parameter optimization dominates.
Analytical estimates based on temperature derivatives indicate that 35–42 % of the differences in GPP and 71–85 % in Reco differences between resolutions can be attributed directly to temperature. Additionally, a linear perturbation analysis confirms the key role of temperature in unresolved topography, while it clarifies that radiation accounts for most of the remaining GPP variance and that e.g. water stress and vegetation types from satellite data add smaller but systematic biases.
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CEC1: 'Comment on egusphere-2026-939', Astrid Kerkweg, 22 May 2026
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AC1: 'Reply on CEC1', Matthias Reif, 27 May 2026
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Dear Astrid Kerkweg,
Thank you for your editorial review and for the clarifications regarding GMD's manuscript requirements. I address your three points below and will incorporate the corresponding changes into the revised manuscript.
1. Model name and version in the title
I will revise the title to: "WRF-VPRM v0.2 (WRF v4.5.2): Sensitivity of CO2 exchange to model resolution and parameter settings over Alpine topography". This follows the convention used in recent GMD papers such as WRF-GC v1.0 (WRF v3.9.1.1) and WRF-ELM v1.0. The corresponding code has been tagged v0.2 on GitHub and persistently archived on Zenodo:
- Workflow & post-processing (inComplexTopo): https://doi.org/10.5281/zenodo.20395509
- Modified WRF v4.5.2 (branch WRF-P): https://doi.org/10.5281/zenodo.20395505
- Modified WPS (branch WRF-VPRM-CLC): https://doi.org/10.5281/zenodo.20395507
Would you like us to promote the version to v1.0 at acceptance, or is v0.2 acceptable for the published version?
2. Persistent archiving of the modified code
On reviewing our existing Zenodo record (previous version v2, 10.5281/zenodo.19997546) while preparing the revision, I discovered that the bundled WRF/ and WPS/ directories in fact contained upstream code rather than our modified forks. I corrected this by archiving the modified branches separately on Zenodo (DOIs listed under point 1 above), each pinned to tag v0.2. The same record has been updated to a new dataset-only version (v0.2, DOI 10.5281/zenodo.20395680) containing only the WRF output, FLUXNET2015, VPRM input, and CAMS data; the modified source code is now cited via the three new code-record DOIs.
The pyVPRM framework used in the paper is the publicly released v3.0 (https://github.com/tglauch/pyVPRM/releases/tag/v3.0); I will cite this specific version explicitly in the revised manuscript.
3. Paper type
I agree with the reclassification from "Model experiment description paper" to "Development and technical paper" and thank you for coordinating this change with the editorial office.
The revised manuscript and Code-availability section will be uploaded at the revision stage, after the public discussion has closed.
Best regards,
Matthias Reif (on behalf of all authors)
Citation: https://doi.org/10.5194/egusphere-2026-939-AC1
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AC1: 'Reply on CEC1', Matthias Reif, 27 May 2026
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RC1: 'Review of: “Sensitivity of CO2 exchange in WRF-VPRM to model resolution and parameter settings over Alpine topography”, authored by Reif et al., reviewed by an Anonymous Reviewer', Anonymous Referee #1, 19 Jun 2026
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General comment:
This study attempts to answer the question of how sensitive the results of VPRM (Vegetation Photosynthesis Respiration Model) simulations of carbon dioxide fluxes are to changes in model resolution and the selection of VPRM parameter settings. Building upon a previous synthetic study, the authors argue that uncertainties in CO₂ fluxes over mountainous regions, stemming from variable resolution, could impact future climate predictions. In the current study, they aim to expand the analysis to a real-world case. To obtain the accurate CO₂ fluxes required for their investigation, the authors evaluate and optimise the VPRM model parameters using observational data from FLUXNET and previously described methodologies to arrive at improved gross ecosystem exchange (GEE) and respiration (RECO) fluxes.
Throughout the text, the authors demonstrate a good grasp of the topic and a fluency in the technical aspects of the numerical model and data analysis. The design of the experiment is sound overall, and the methods and tools employed are appropriate. The language is of high quality, figures are well prepared (some might use larger fonts).
Nevertheless, the paper suffers from some major deficiencies. The text's structure is chaotic, with a long and rambling introduction and an undisciplined approach to separating methods, results, and discussion. This, together with repeated information and five appendices, makes it difficult to follow. Please see below for some suggestions about restructuring, but note that these are merely indicative, as some sections require a complete overhaul (e.g. the introduction).
Most importantly, I believe that the authors are attempting to draw significant conclusions from a dataset that is too limited. With only 24 days of simulations selected to represent cloudy and clear conditions in equal measure, the authors are left with a very limited dataset on which to base conclusions about a highly dynamic process such as ecosystem CO₂ exchange. This makes the robustness of the presented results doubtful at best, a fact of which the authors are somewhat aware (L395–406). In the text, the authors suggest a multi-year analysis (L400–404); however, this might not be necessary. If a climatologically regular year is chosen, a single 365-day period should represent seasonal changes adequately. If this is computationally too expensive, perhaps a comparison between winter and summer would be sufficient, although with shorter periods it might be harder to achieve a balance between cloudy and clear conditions.
In its current form, I suggest rejecting the paper and requesting another complete review round after all the listed points have been addressed.
Specific major comments:
The introduction shows that the authors have dedicated time to studying a broad range of topics, but the themes described change too radically. The paragraphs describe, in order, the terrestrial carbon sink, observation data, night-time biases in mountainous terrain, CAMS CO₂ fluxes, the influence of complex topography on atmospheric dynamics and various ecosystem models (three paragraphs), and the influence of topography on CO₂ fluxes. Afterwards, the description of the experiment is slightly more structured. Please shorten and rearrange the introduction, focusing only on information relevant to the study.
There are also some important literature references which the authors should not omit, given the topic. Ahmadov et al. (2007) describe the first implementation of the WRF model with the VPRM, which later became WRF-GHG (see the remark below regarding L91). Furthermore, Pillai et al. (2011) have studied CO₂ simulations with WRF-VPRM over the complex terrain around the tall tower on Ochsenkopf mountain. While not alpine, the authors might also note that the analysis of model performance at varying resolutions was discussed there too, albeit the fluxes themselves were not the primary focus.
I am also uncertain of the usefuleness of CAMS products in the study. While the authors reasonably state that they are using it for comparison purposes, they also refer to a study by Custodio, Borrego and Relvas (2022), which focuses on the atmospheric CO₂ concentrations of the CAMS EGG4 global reanalysis product. However, in other parts of the text, global forecasts are mentioned (L53 and L62 refer to 9–10 km resolution, whereas EGG4 is much lower at 0.75° x 0.75°), which are a different product, for which the results of the Custodio et al. study might not be relevant. The authors do not seem to be aware of the differences between them and simply refer to the data as CAMS. The data product used must be clearly identified. Also, while the results may be of some interest, considering the minor role of CAMS in the discussion, the authors should seriously consider moving most of these results to the supplement.
Other comments:
L09: DEF would be a more natural acronym since length is not an issue to other sets (ALPS, SITE)
L22: “resolution-induced errors govern NEE uncertainty” – this suggests like resolution is the main driver of the overall uncertainty. This is too general, there are other significant sources of error for annual NEE. Please reword that this relates only to results of this numerical experiment.
L25: which temperature is meant here? Please be precise.
L68-69, and in other places: Throughout the text authors conflate “plant functional types” (PFT) with “vegetation classes”, but the distinction is not made clear. In all of the past studies describing VPRM and WRF-VPRM, "vegetation class" is used consistently. PFT is meant to distinguish groups of vegetation meant to behave same way in terms of process, whereas vegetation classes typically describe dominant ecosystem type over a certain area – related to what eddy covariance tehcnique is able to measure. I suggest authors to refrain from using PFT and use the more appropriate term "vegetation class" -- consistent with previous literature.
L83-84: In the present study… -- this fits better in “Discussion”
L91: “…CO2, CH4, and CO as passive tracers”. Historically, WRF-VPRM was developed only for CO2 (Ahmadov et el. 2007). Augmented version with three tracers is more appropriately referred to as WRF-GHG. See section 2.2 in Beck et al., 2013. In the context of this current study, perhaps WRF-GHG would also be more appropriate, but WRF-VPRM is acceptable.
L111-112: 50% of the global land surface seems excessive in the context of CO2 fluxes. Does it mean that over 50% of the land area exhibit significant biases of CO2 fluxes in the climate models? Consider dropping the reference.
L121: Before this paragraphs the text feels chaotic and disjointed. Intro needs overhaul. See major comments.
L145: Single days (the classic case study) – Too general. I am not aware of single days being “classic case study”. Please rephrase.
L147: How do the authors assure that the days selected are unbiased and representative? Conditions on selected days could have been easily compared against climatology. One could argue that 12 days is a sufficient sample size to randomize the selection and avoid bias, but the issue is that CO2 fluxes are seasonally varying with large variability, which effectively reduces the sampling to 3 per season. The results could be unbiased, but quite robustness of the results will remain in question with such a limited sample.
L151-153: (…), making VPRM particularly suitable… -- move to introduction
L154: Factor 6x between d01 and d02 is not a typical choice for WRF. The model authors recommend "using odd numbers, and typically only advise to use either a 5:1 or 3:1 ratio".. Did the authors evaluate the consequences of using the even, hight ratio between domains? What was the spacing between domain boundaries? Distance between domains is recommended to diminish the boundary distortions. Authors only write that smaller domains were "same size". Please be precise.
L158: 1. Was pressure data used, or model-level data? ERA5 comes in both, selection determines the vertical resolution of the input data. 2. What was the thickness of the lowest layer? 3. How many levels were below 3km altitude on average?
L161: “Each run started…” -- What was the rationale behind this? Please note that this is the same setting as Ahmadov et al. proposed in 2007 (see par. 25, page 5 in their study), I suggest adding the reference here.
L167: “are mapped to plant functional types (PFT) of VPRM” – 1. See comment to L68-69 above. 2. This acronym is already explained earlier in L68. In other places, however, the authors skip explaining acronyms and refer to the Table D8 (e.g. NSSE). Please make it consistent. Also, I suggest to move the acronym table as the very first appendix.
Figure 2, caption: “Areas with a standard deviation of subgrid-scale topography of STDTOPO < 200 m” -- Consider calling that "area of interest" or "area of analysis" for easier reference in text.
L205: This detailed description shows the authors carefully applied the formulas for VPRM, which is commendable. Scientifically, however it doesn't bring new knowledge. For paper brevity, I would recommend moving most of this section to the supplement, leaving only a short description of the VPRM model and underline significant differences to previous applications -- this is done in the next subsection, so both can then be merged.
L219: Per my understanding this paragraph is about a minor unit change with linear scaling, and results should be 1:1 identical. If I’m not mistaken – again, for brevity, consider moving to supplement, with reference here (unless the whole section is moved, see above).
L278: “There is no dedicated publication on the VPRM parameters that are currently implemented in WRF-VPRM.” – not entirely precise; to the best of my knowledge, the parameters for US are still the original ones from Mahadevan et al., so for default values the study of Mahadevan et al. can be used as ref; for Europe these were implemented in Beck et al. 2011, however the authors are correct that there is no dedicated description on how the European callibration was made.
L290: ‘… are minimized with a cost function’: Please provide the formula
L300-301: ‘To partly account for this, a PFT-specific Topt was determined for the Alps. T2m and NEE data from nineteen FLUXNET sites…’ – note that Fig 2 shows 5 sites. Table D2 shows it's 15 sites in the Alps. Please clarify and give reference to D2
L323: Method of interpolation?
L333, all sections: This, while interesting, is less important for the scientific part. Consider moving to the supplement for brevity.
L367-371, and Figure 3: The authors use it as an example plot, but it depends on the T2m simulated in the model, so rather fits into a "Result" section. My suggestion would be to move it there.
L375: ‘IT-MBo was selected because it exhibited the best overall model-data agreement’ -- I do not think this is methodologically appropriate. Rephrase. Also: consider bringing all results (E2-E5) into the main text, and Tables D5 and D7. The results form the basis of evaluation and are critically important considering the study title.
L388: ‘Detailed MB and MAE values are listed in Appendix D (Table D5).’ – repeated info, already given in previous paragraph
L395-399: This goes directly towards my major comment about robustness. I’m sorry but in my mind this undermines the whole analysis.
L400-406: Also see my major comment. Unrelated: this fits more into the Discussion section.
L416-419: This fits into Methods section.
L420: “warmer T2m” – should be “higher T2m”.
L432: ‘resulting from CAMS being higher than’ – I assume it should be ‘CAMS CO2 fluxes being higher…’
L433: ‘Figure 6 shows the spatial distribution of S↓ and RAD at 54 km and 1 km grid spacing for a morning hour when differences are most pronounced.’ – again, this might seem like cherry-picking.
L440: ‘Under clear-sky conditions at 1 km, DF reaches 64% and 54% of ALPS GPP and Reco, respectively, …’ – usually the older value, even if imperfect, is treated as reference. Consider describing ALPS as percentage of DF.
L441: ‘This difference arises from…’ – move to Discussion please.
L444: ‘This apparent improvement…’ -- same.
L472: ‘While CAMS employs a distinct biosphere model…’ – move to Methods (or Discussion)
L477: Overall – same.
L482-489: This is Intro.
L603: ‘A feasible approach to reduce structural resolution effects is a subgrid-scale flux…’ – The authors write with a high degree of certainty, however it is speculative whether such a parameterization would in fact fix the lack of resolution. Similar issues faced by climate models related to convection and other scale-sensitive phenomena have shown that deficiencies are to be expected. So until demonstrated, I gently suggest to soften the language somewhat, until method is demonstrated.
L612: ‘bias CO2 update, with a direction’ – change to ‘sign’
L617: ‘(Q2) At fine horizontal grid spacing (O(10 km)), parameter choice is the’ – consider expanding what parameter is meant.
L622: ‘shows that site-specific parameters’ – ‘shows that site-specific (i.e. adjusted based individually for each site) parameters’
References:
Ahmadov, R., C. Gerbig, R. Kretschmer, S. Koerner, B. Neininger, A. J. Dolman, and C. Sarrat (2007), Mesoscale covariance of transport and CO2 fluxes: Evidence from observations and simulations using the WRF-VPRM coupled atmospherebiosphere model, J. Geophys. Res., 112, D22107, doi:10.1029/2007JD008552.
Beck, V., Gerbig, C., Koch, T., Bela, M. M., Longo, K. M., Freitas, S. R., Kaplan, J. O., Prigent, C., Bergamaschi, P., and Heimann, M.: WRF-Chem simulations in the Amazon region during wet and dry season transitions: evaluation of methane models and wetland inundation maps, Atmos. Chem. Phys., 13, 7961–7982, https://doi.org/10.5194/acp-13-7961-2013, 2013.
Beck, V., Koch, T., Kretschmer, R., Marshall, J., Ahmadov, R., Gerbig, C., Pillai, D., and Heimann, M.: The WRF Greenhouse Gas Model (WRF-GHG), Technical Report No. 25, Max Planck Institute for Biogeochemistry, Jena, Germany, , 2011.
Pillai, D., Gerbig, C., Ahmadov, R., Rödenbeck, C., Kretschmer, R., Koch, T., Thompson, R., Neininger, B., and Lavrié, J. V.: High-resolution simulations of atmospheric CO2 over complex terrain – representing the Ochsenkopf mountain tall tower, Atmos. Chem. Phys., 11, 7445–7464, https://doi.org/10.5194/acp-11-7445-2011, 2011.
Citation: https://doi.org/10.5194/egusphere-2026-939-RC1 -
RC2: 'Comment on egusphere-2026-939', Anonymous Referee #2, 26 Jun 2026
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The Vegetation Photosynthesis and Respiration Model (VPRM) is a light-use efficiency model that estimates carbon dioxide exchange between the atmosphere and the terrestrial biosphere using satellite imagery and meteorological reanalysis data. It is frequently coupled with atmospheric transport models such as WRF. In this study, the authors investigate how VPRM results are influenced by model resolution and parameter choice in a topographically challenging environment, namely the European Alps. This is a relevant research question, as VPRM is widely applied in carbon cycle studies across Europe.
The authors conclude that, at high spatial resolution, parameter optimization has a larger impact on model performance than spatial resolution itself, whereas at 50 km resolution unresolved topographic effects dominate. They further show that differences between resolutions can largely be attributed to temperature. This result is plausible, as VPRM is primarily driven by incoming shortwave radiation and surface temperature, the latter of which is strongly influenced by topography.
Overall, the analysis is methodologically convincing. However, the manuscript is written in a way that makes it difficult to follow the main arguments and identify the key findings. I believe this issue can be addressed, but it will require substantial revision.
Readability could already be improved considerably by shortening sentences and removing redundancies. In addition, very long citation lists (e.g., Segura-Barrero et al., 2025; Jose et al., 2025; Zhao et al., 2023; Huggannavar and Indu, 2023; Raju et al., 2023; Parazoo et al., 2022; Callewaert et al., 2022; Gourdji et al., 2022) and the excessive use of acronyms should be avoided.
In the following, I distinguish between structural and methodological comments.
Structural comments
- The introduction could easily be shortened by about one-third without losing relevant information. At times it reads more like a review article than the introduction to a research paper. For example, the P-model is described in detail, despite the authors explicitly stating that it is not used in this study. This is followed by an extensive description of VPRM, including information that is not directly relevant to the research question. Similarly, the paragraph on CAMS introduces numerous acronyms and model names that many readers are unlikely to be familiar with. I encourage the authors to carefully review this section and remove material that is not essential for understanding the study or its motivation.
- The distinction between methodology, results, and discussion is often unclear. Equations (13)–(15), for example, belong in the Methods section and should be introduced and explained there. After reading the methodology, the reader should understand what analyses will be performed and why they are necessary.
- The Results section would also benefit from a stronger focus on the findings that are most relevant for the discussion and conclusions. At present, it is easy for the reader to lose track among the many numerical values and abbreviations. The authors should identify the key results that support their conclusions and emphasize those more clearly.
Methodological comments
- Temperature optimum calculation: The optimum temperature is indeed an important parameter in biogenic flux models and is often not treated with sufficient care. I therefore appreciate that the authors investigate this aspect. However, the proposed approach has important limitations. Fitting average NEE as a function of temperature does not necessarily recover the optimal temperature for GPP for several reasons. First, NEE depends on both GPP and ecosystem respiration (Reco), each of which has a strong temperature dependence. Second, this approach neglects the influence of other important environmental drivers, particularly vapor pressure deficit (VPD). Since the manuscript also investigates the sensitivity of the results to temperature, I wonder to what extent these findings depend on the estimated optimum temperature, as this parameter directly affects the shape of the temperature response function in the VPRM GPP formulation.
- DF VPRM parameters: In line 280, the authors note that the standard WRF parameterization suffers from shortcomings due to the one-step fitting procedure. However, Glauch et al. (2025), which is cited in support of this statement, also proposed an updated parameterization for Europe. Why did the authors retain the older parameter set instead of adopting the revised version?
- SITE parameters: I am not convinced that this parameter set adds much to the paper. As I understand it, the parameters are calibrated and evaluated using the same site, meaning the results primarily demonstrate goodness of fit rather than predictive skill. If this interpretation is correct, I would place less emphasis on this comparison.
- Sample size: I assume that the decision to analyze only 12 sunny and rainy days was motivated by computational constraints. Under those circumstances, this approach may be justified. However, I wonder how much uncertainty is introduced by this selection. Have the authors evaluated the sensitivity of their conclusions to the number of sampled days, for example by repeating the analysis with only 8 or 10 days?
- CAMS comparison: I am not convinced that the comparison with CAMS substantially strengthens the manuscript. It is not mentioned in the abstract, and in the discussion the only conclusion drawn is that: "Comparison with CAMS confirms that WRF-VPRM results fall within a realistic range for the annual carbon budget, despite differences in seasonal cycle and meteorological drivers." This finding is not particularly surprising, given that the model already reproduces the station observations with reasonable accuracy. In my opinion, this comparison could be omitted, as it increases the length and complexity of the manuscript without adding substantial insight.
Overall, I believe the study addresses an important and relevant research question, and the analysis is generally sound. If the authors adequately address the comments above I’m happy to see the (revised) manuscript being published.
Citation: https://doi.org/10.5194/egusphere-2026-939-RC2
Data sets
WRF-VPRM Simulations in Complex Topography: Model Configuration and Sample Output Data Matthias Reif https://doi.org/10.5281/zenodo.18481849
Model code and software
Github repositories for model configuration and postprocessing Matthias Reif https://github.com/Matthias-Reif-PhD?tab=repositories
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Dear authors,
in my role as Executive editor of GMD, I would like to bring to your attention our Editorial version 1.2: https://www.geosci-model-dev.net/12/2215/2019/
This highlights some requirements of papers published in GMD, which is also available on the GMD website in the ‘Manuscript Types’ section: http://www.geoscientific-model-development.net/submission/manuscript_types.html
In particular, please note that for your paper, the following requirements have not been met in the Discussions paper:
Please note, that the version number or specific identifier for WRF-VPRM is missing in the title. Furthermore, especially the modified code needs to be persistently archived, and therefore please also store the "modified WRF-VPRM source code, including the extensions for parallel execution of multiple parameter sets and the analytical tempera-
ture derivative implementations", which are sofar only available on GitHub and the pyVPRM framework in a permanent archives as e.g., zenodo.
Additionally, the paper type "Model experiment description paper " is specificially for papers describing the layout of model experiments, which should be executed by a variety of modeling groups using many different models (i.e.., CMIP-like activities). As you paper does not fit into this category, I will ask the editorial office to move your paper to the "Development and technical paper" section.
Yours, Astrid Kerkweg (GMD Executive Editor)