This publication highlights the effects of wood heating on air quality, which is important for our health and also for our climate.  Experimental data were collected at a rural site where many wood-fired heating systems are in operation during the winter.  Special attention will be given to particle properties that are relevant to the radiative forcing of these anthropogenic aerosols.

The work is important to the scientific community because it quantifies the existing particulate air pollution at this site and describes the properties of the particles that will allow understanding and improved modeling of their effects.

I recommend the paper for publication after the authors address the issues listed below.

One conceptual weakness in the interpreted data is the following:

An important metric used in the paper is PM1, which was calculated from the number-size distributions using density and shape assumptions. However, the size spectra were only recorded up to 600 nm (or 800 nm), and if one looks more closely at e.g. Figure 3f, one clearly has to assume that there is a substantial particle volume between 600 nm (800 nm) and 1000 nm. This does not seem to be taken into account and leads to a significant bias towards too low PM1 values. As a first step, the measured size distributions should be extrapolated into this gap by making appropriate assumptions (log-normal surface distribution or volume distribution?). A discussion and estimation of the resulting errors is mandatory.  

Another important problem is that eq 14 is wrong (see below).

Specific comments (in order)

Line 21: "more common in rural areas". Is this true? In some cities, wood is also used for heating and dominates air quality in winter.

Lines 40-44: RWB is also important for the health of the local population. This could be mentioned in the abstract. Out of curiosity, has there been an epidemiological study of health effects at the site? Could be informative.

Line 95, end of intro: Suggestion to add a few lines pointing out technical solutions to make wood burning cleaner (better certified stoves, appropriate fuel, burning conditions, electrostatic precipitators).

Lines 113-114: The difference in m a.s.l. is 200 m and contradicts the information in Fig. 1.

Line 163: "Contribution from fibers": Please be more precise. On the one hand directly, but probably also by condensation of semi-volatile gases on the fibers.

Lines 164-169: This is a can of worms and very unsatisfactory. On the one hand, a site-dependent empirical correction for multiple scattering effects in the filter (C) is used, and on the other hand, the harmonization factor is used. Both factors are determined empirically and influence each other. This makes it difficult to compare different instruments on different types of aerosols. A more thorough discussion is needed to disentangle the two factors (C and H). In addition: I also assume that C and H are wavelength dependent - correct? Please clarify.

Line 180, Table 1: What is the weighing procedure for PM10? The table is not complete. I am missing information on offline TCA, ion chromatography, levoglucosan. Was an impactor used in the SMPS that allows the correct correction for multiple charging? This is essential for correct volume determination. Why does one SMPS measure only up to 600 nm and the other up to 800 nm? However, the aerodynamic diameter is given. How was this converted?

Line 182, eq 2: why does it say "fraction in PM"? this is misleading because a fraction is unitless - the rest of the equation is not unitless...

Line 188: Suggest writing PM0.8 or PM0.6 instead of PM1.

Line 210, Figure: I expect large systematic errors affecting the slope. Please discuss.

Line 214: Is OA_MPSS = PM1 ? please be consistent and use the same names.

Line 222: Is it justified to assume that transmission, albedo, backscatter fraction are constant, i.e. not wavelength dependent? For which part of the electromagnetic spectrum is this true?

Line 292: Is it EC or BC (EC is present with lower time resolution)?

Line 300, Fig 3: the color for "unstable" is hard to distinguish, perhaps better in green. Fig 3b: At what wavelength was BC measured? Fig 3f: here the spectra go up to 850 nm. an additional plot of the volume size distribution would be helpful.

Line 327, caption Fig. 4: the black points (outliers) are not visible.

Line 332, Fig. 5: ditto

Line 335 and elsewhere: given the relatively large uncertainties, it makes no sense to give the values so precisely. Here 1100 mM-1 would be appropriate.

Line 347, eq 12: This relationship is general and one could remove the BC here.

Line 351, eq 13: The exponent is an equation and therefore misleading. Just write -1 as the exponent.

Line 335, eq 14: I think this equation is clearly wrong. It should be: b_abs.BrC(l1)=b_abs(l1)-b_abs(950)*(l1/950)^-1.

Line 366, Fig. 6: Will this figure change if eq. 14 is changed? Depending on this, it will also lead to an adjustment of the discussion (e.g. lines 369-377).

Line 394: Will the "photochemical process" lead to an increase or decrease of AAE_BrC?

Lines 403-420: Again, the problem with PM1: How much does the missing volume affect the MAC values? I would like to see a presentation and discussion of the systematic errors.

Line 429: Regarding the measurement conditions: How were the particles sampled to the instruments (sampling conditions, at what temperatures and thus relative humidities were the particles measured)?

Line 450: The beta should be a_s.

Line 453: I have recalculated the RF values in Fig. 9 graphically and get about 20% lower values. Please check the integration. Note that in Fig. 9 the wavelengths are not equidistant as shown!

Line 460,461: two times: inverse square meter

Line 466: the lensing effect was not described before. Have you compared the MAC_BC with literature values? Should it be higher in this study?

Line 470, Table 3: The min and max values are not very meaningful because they depend on the choice of the averaging interval. Better would be e.g. quantiles 

Line 489, 490: Consider (again) the number of significant digits. Put the units after the whole expression: e.g: 71 +- 56 ug/m3.

Biomass burning emission is a hot topic in Air Quality in Europe. Biomass burning, mainly related to residential heating has recently increase due to the incentives to reduce greenhouse emissions. These emissions can be very important in medium size cities and in rural areas, and may have impact on both health and climate. As shown in the present article, this can be of great interest in rural areas frequently affected by thermal inversions. Moreover, there is growing interest in evaluating the optical properties of carbonaceous aerosols emitted by biomass combustion. The manuscript corroborated the importance of this source at rural areas and demonstrates the influence of coating of BC by OA in absorption and therefore on atmospheric warming. 

This is a 2 months period campaign carried out in the village of Retje, in Slovenia. A complete set of instrumentation was settled at the village and at a reference location, 150 m higher. Instruments comprised: Aethalometers, MPSS, and CPC. Ions and EC/OC were determined at filters collected by high volume samplers. At the village site a total carbon analyzer was also used.

The paper is of interest and deserves to be published in ACP although there are some aspects that can be improved, mainly related to the uncertainty in the estimation of OA. 

As stated in the manuscript, estimating OA hourly concentrations by subtracting BC and ions (measured in PM_2.5 and PM₁₀, respectively) from the PM₁ mass calculated form MPSS could be the largest source of uncertainty: 1) by the different sizes measured / sampled; 2) the MPSS in Retje measured from 10-800 nm; 3) because the ions were offline estimated in PM₁₀ filters collected every 12h and a constant contribution of ions to PM₁ has been assumed, affecting the time variation of OA. Ions and EC/OC mainly concentrates in PM₁ but presence in the coarser fraction cannot be discarded.  It is true that there is a very good correlation between PM10 and PM1 derived from MPSS, indicating 90% of PM₁₀ is in the PM₁ fraction as an average; but in some cases, with high PM concentrations, PM₁ accounts for around 70% of PM₁₀ and then there is an important contribution of coarse PM that will affect the OA estimation. The authors compared OA_MPSS and OA_TCA and concluded that the good correlation corroborates the adequacy of the method used. However, it must be considered that, in both cases, OA/OC ratios used have been estimated by comparing the OA estimated from MPSS with the OC of filters. Therefore, the good correlation between OA_MPSS and OA_TCA only demonstrates a good correlation between OCtca and OC filters, but does not provide evidence on the suitability of the method used for estimating OA. 

This uncertainty in the estimation of OA may have a high impact on the results and conclusions. Thus, it will influence the estimation of MAC_OA. Then, I considered that more info about OA uncertainty should be provided. 

Minor corrections

Line 139. Add refence for TCA

Line 180. This Table can go to Supplementary. Information on inlets size cut should be added

Line 270: Table 2. Can you add the % of hours for each category during the sampling period? Or just shortly describing the frequency of the stability categories in the text.

Line 282 (and Fig.3): Does OA refers to OAmpss? It should be clearly stated that OA refers to OAmpss in the manuscript.

Lines 287-289: PNC is very similar for strong inversion and unstable atmosphere. 

Line 312-317. Little discussion about ΔPNC and PNSD; I understand this is not the topic of the articles. PNC measurements have been mainly used for deriving PM1 and hourly OA. However, I would add an explanation abut similarity of ΔPNC for N10-50 during the three categories

Figures 4 and 5. Captions: Please, remove “black dots” at the end of the caption. Check whiskers: do represent 25-75%?

Figure 6. I do understand the increase of absolute concentrations during strong inversions. How do you explain the increase of the relative contribution of BrC with respect to BCtotal? Is it because strong inversions are mainly produced at night when domestic heating emission are more important? Or because you assume all BB emissions are local while traffic emissions are also external? Based on the results obtained in the paper, do you believe this source apportionment is realistic? Have you compared with BC SA at the reference site?

Comments to the manuscript: “Optical properties and simple forcing efficiency of the organic aerosols and black carbon emitted by residential wood burning in rural Central Europe” by Cuesta-Mosquera et al.

In this manuscript the Authors present the results from a winter measurement campaign performed in a rural European site strongly affected by RWB emissions and characterized by strong thermal inversions. The site location and emission characteristics allow for a robust optical characterization of RWB OA. The results from a simple forcing efficiency estimation are also reported.

The manuscript is well written and the results consistently reported. The paper can be published in ACP after some minor revisions reported below.

• 7, line 171: Has the article about the harmonization factor H been published at the time of this review? Can the authors provide some more information? One reference about H (1.76) is Savadkoohi et al., 2023 (https://doi.org/10.1016/j.envint.2023.108081).

• In this manuscript the signal at 950 nm is used as reference to calculte eBC, MAC and to separate BC and BrC contribution to absorption in the 370-880 nm spectral range. Normally the 880 nm signal is used for these objectives as a compromise between excluding the absorption from OA and having a good signal-to-noise ratio. By using the 950 nm as reference, automatically a small OA absorption at 880 nm is allowed, whereas OA absorption is usually (in literature) excluded at this wavelength. Can the authors provide some more details about the choise of using the 950 nm?

• It might be more useful to present in figure 3d the first derivative of the potential temperature with horizontal lines highlighting weak, strong, unstable, neutral conditions.

• Equation 13: Is there any specific reason why an AAE of 1 was used?

• 17. Lines 379-389: Here the authors present the Angstrom exponent of BrC absorption that was calculated between 370 and 590 nm. Thus, the BrC absorptions calculated at 660 and 880 nm were excluded from the BrC AE calculation. In fact, the authors explain that if the BrC AE is calculated between 370 and 880 nm, then a 50% overestimation of BrC absorption at 370 nm (obtained from equation 14) is observed.

             However, it would be useful if the authors could provide more details about how they “simulated” the BrC absorption at 370 nm using                 the calculated BrC AE. If I well understand, the “simulated” BrC absorption at 370 nm was calculated from the BrC at 880 nm using the                 BrC AE from 370 and 880 nm and this “simulated” BrC absorption at 370 nm oversestimates by 50% the BrC absorption obtained using               equation 14. Consequently, the best simulation of BrC absorption at 370 nm was obtained using the AE from 370 and 590 nm. Thus,                     the BrC absorption at 370 nm was simulated from the BrC absorption at 590 nm using the AE calculated from 370 and 590.

             Is the procedure described above the one used by the authors?

It would also be useful if the authors could explain in more detail the reasons why the absorptions at 660 nm and 880 nm were reasonably excluded. The authors report that this could be due to the presence of internally mixed aerosol particles. However, since the procedure described here and used to separate the absorption by BC and BrC is widely used, more details regarding why one needs to go down two wavelengths (from 880 to 590 nm) to calculate the AE should be given.