Manuscript egusphere-2025-1225 by H. Wiedenhaus et al. reports model results of the COSMO-MUSCAT chemistry transport model on particulate matter concentrations during winter months, with a focus on emissions from residential heating. Modeled organic matter concentrations are compared against measurements at three observation sites with specific aerosol instrumentation. The employed source apportionment by tagging method is robust and carefully applied (only for primary components). The study investigates the impact of SOA formation from anthropogenic VOCs related to wood burning emissions. A weak component of the model system is the emission inventory for residential heating. The study should try to better identify and isolate wood burning as the missing source of primary/secondary OM. The sensitivity tests are well performed but it is difficult to evaluate the impact on anthropogenic SOA concentrations and their spatial distribution. I strongly recommend the addition of one more sensitivity test including more detailed wood burning emissions. The conclusions are based on the findings of the model study and future directions are well formulated.

Specific Comments:

1.) Introduction (P2, line 28-34): Suggest rewriting the paragraph on transboundary transport of pollution to Germany. Expand on the influence of long-range transport from eastern Europe, also including reports from EMEP. The sentence in line 28 (“the inflow of air masses from the east”) is not logical and should be deleted.

2.) Introduction (P2, line 54-58): Add a brief description of the TRACE project, its objectives and how this study addresses the project’s objectives.

3.) Model description: how frequent is the exchange of variables between the meteorological and the chemistry-transport component? What is the expected advantage of the online coupling specifically for this study compared to using an offline coupled CTM?

4.) Model description: it is stated that the GRETA emission database was provided with resolution of 0.5 km x 1 km. The usual GRETA grid has a resolution of 1 km x 1km. Why did you choose this resolution and was any reprojection on the COSMO grid required?  It would be good to mention the specific temporal profile for other combustion (i.e., for residential heating).

5.) Emissions: Different years of the emissions were used as emissions for 2021. Was something done to adjust for year-to-year changes in emissions? How is the expected variability between the years for the different source types?

6.) SOA formation (P 6, line 160-170): A table should be added with a list of the different model surrogates of SOA precursors from the different parent VOCs. In particular, the precursors of anthropogenic SOA should be detailed. If possible, supplement the relevant reactions and stoichiometric yields of the two pseudo-products.

7.) Comparison model-measurement: clearly state that the statistics of the model-observation comparison are given in Table A1. The evaluation should be expanded by calculation of the normalized mean bias (NMB) and FAC2 (fraction of modeled values within factor 2 of measured values). When discussing model underestimation always include the relative bias as NMB (RMSE represents the model error in terms of bias and correlation). The reference to Stern et al. (2008) is not adequate as it refers to PM10 which is much more determined by dust resuspension and Saharan dust events than PM2.5. There are several AQME intercomparison studies which could be cited for discrepancies among models and between modeled and measured concentrations. For PM2.5, different treatment of the formation of secondary aerosols is certainly the most important reason for discrepancies between models. On P10, line 257-259, it is discussed that increased heating and limited mobility caused underestimation of “total pollutants”. I would expect that the two activities have opposite effects on certain pollutants, for example NO2 concentration might decrease due to limited mobility whereas PM2.5 concentrations might increase due to more heating in households. The sentence needs to be revised.

8.) Organic Matter (P 13): Figure 4 shows good agreement among Sunset offline and Sunset online. It should be discussed why OM from Sunset agrees with AMS at Kosetice but not at the other sites. Further it should be discussed which of the measurement methods should serve as the guideline for comparison of the modeled OM (OM in PM2.5 plus total SOA plus OM from outside the domain). In the text, the terms AMS and ACMS are used interchangeably. It is unclear whether ACMS is an additional instrument or combined with AMS. If it is a separate instrument, why are OM measurements of ACMS not included in Figure 4? At least, it should be made clearer in the text.

9.) The paragraph on P 14 (line 316-320) should be rephrased. “The discrepancy in modelled PM2.5 concentrations”  probably means discrepancy between modeled and measured PM2.5 concentrations. Background PM2.5 is hardly ever driven by elemental carbon since EC concentration are usually rather low (except near sources). Sulfate and nitrate are more likely candidates for mismatch with observed PM2.5, thus the agreement for these components should be stated as well.

10.) The numbering and headers of the sections after 3.3 (“Source attribution …”) appear to be random and are not well motivated. I suggest bracketing the sections that follow under a “Discussions” chapter (section 4). The second part of section 3.3 could be split off as a discussion section on biomass burning / wood combustion. Together with section 3.4 (“Effects of COVID-19”) and section 4 (“anthropogenic secondary organic aerosol”) this would form the new discussion chapter.

11.) Anthropogenic secondary organic aerosol (P 20): The study of Bergström et al. (2012) was first and should appear first in this section. It would be good to structure the discussion related to publications on SOA modeling in chronological order, as there have been drastic developments in the treatment of anthropogenic SOA in the last two decades. Can the IVOC emissions be implemented in your model such that IVOC condense to pre-existing OM depending on their volatility or undergo atmospheric aging?

12.) Sensitivity study results: as in my previous point 8, I wonder which observed metrics / measurement instrument should be used to evaluate changes in mean OM concentrations from the sensitivity tests? On P 22, line 502-510: (a) give absolute OM increment for Melpitz, (b) refer to Table 4 again, (c) discuss that OM from AMS is overestimated with S3 at Frydlant. In Figure 9, denote error bars for Sunset offline OM which considers instrument uncertainty and OC-factor uncertainty and denote error bars for AMS PM1 data.

13.) Sensitivity study results: the discussion of the sensitivity results for CSL emissions and phenol SOA leaves some open questions. Which of the scenarios (base, S1-S3) is now best in reproducing SOA spatial distribution? Figure 10 shows that S3 increases modelled OM in other areas but not around the three study sites. This probably reflects that absorption of SOA to existing PM happens in places where the emissions of PM are already high. This would indicate missing primary OM emissions given the underestimation of measured OM at the sites.

14.) To test this hypothesis, I suggest to conduct an additional sensitivity test with more detailed residential combustion emission data for the Czech Republic as used in Bartik et al. (2024).

Technical corrections:

• P3, line 57: replace “identify PM sources” by “identify primary PM sources”.
• P3, line 61: give long name of TRACE and provide web site.
• P5, line 125: resolution should be given in km x km. Same holds for the resolution of CAMS-REG-v5 stated in the next line.
• P12, line 267: replace “below 3 km” by “below 3 km height”.
• Figures: captions of Figures 5-10 denote “elemental carbon < PM2.5” or “organic matter < PM2.5”. This is not common terminology. Please replace by “in PM2.5” if that is the meaning of “<”.