the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
| 13 Mar 2026
Implementation and Evaluation of an Observation-Constrained Secondary Organic Aerosol Parameterization in MOZART–GOCART Chemistry in WRF-Chem
Abstract. A computationally inexpensive, observation-constrained parameterization for Secondary Organic Aerosols (SOA) formation is implemented and tested in the default MOZART–GOCART (MOZCART) chemical mechanism of the Weather Research and Forecasting model coupled with Chemistry (WRF-Chem). The outcomes were evaluated against hourly observations of SOA, Organic Aerosols (OA) and Fine particulate matter (PM2.5) over Delhi during November 2024. Sector-specific Emissions ratios (ERs) derived from in-situ Volatile Organic Compounds (VOC) measurements in Delhi were used, with values of 77 ± 5, 130 ± 13, and 60 ± 9 ppbv VOC/ppmv CO for transportation, biomass burning, and industry-dominated plumes, respectively, to represent SOA formation from anthropogenic and open biomass burning precursors. The modified MOZCART scheme reproduces the temporal variability, with a monthly mean simulated concentration of 53 ± 24 µg/m3 compared to an observed mean of 83 ± 43 µg/m3 (RMSE = 58.2 µg/m3; MFB = −0.53). Inclusion of SOA parameterization substantially improves total organic aerosol (OA), increasing mean OA from 48 to 101 µg/m3 and reducing normalized mean bias from −57.8 % to −19.1 %. PM2.5 predictions also improve, with mean concentrations increasing from 151 to 203 µg m⁻³ and mean bias reduced by ~54 %, alongside better reproduction peak pollution events. Intercomparison with other WRF-Chem mechanisms shows that MOZCART achieves SOA performance comparable to the more complex MOZART–MOSAIC scheme (RMSE = 58.2 vs. 54.8 µg/m3) and substantially better than RADM2–SORGAM, while being ~5.3 times faster than MOZART–MOSAIC. These results demonstrate that the proposed simplified SOA parameterization provides an effective balance between accuracy and computational efficiency and can be effectively used in operational air quality forecasting over highly polluted urban regions like Delhi.
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Status: final response (author comments only)
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RC1: 'Review', Anonymous Referee #1, 23 Mar 2026
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RC2: 'Reply on RC1', Anonymous Referee #1, 23 Mar 2026
A correction to my review: The relevance statement is incorrect, as I accidentally took it from ACP instead of GMD, apologies. The rest of the comments stand, including the broader evaluation needed and the final recommendation.
Citation: https://doi.org/10.5194/egusphere-2026-1302-RC2 -
AC1: 'Reply on RC2', Rajmal Jat, 12 May 2026
Dear Reviewer,
On behalf of all co-authors, I am submitting our responses to your comments. Please find attached the response document for your reference. We sincerely thank you for your constructive comments and suggestions. We have carefully addressed all the points raised and will revise the manuscript where appropriate during the resubmission stage.
With regards,
Rajmal Jat
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AC1: 'Reply on RC2', Rajmal Jat, 12 May 2026
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RC2: 'Reply on RC1', Anonymous Referee #1, 23 Mar 2026
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RC3: 'Comment on egusphere-2026-1302', Anonymous Referee #2, 14 May 2026
The manuscript presents a simplified observation-constrained SOA parameterization implemented in MOZCART within WRF-Chem and evaluated over Delhi during November 2024. The work is relevant, however, the parameterization currently relies on several strong assumptions (e.g., 100% SOA yield, OH-only oxidation, constant VOC/CO ratios, simplified lumping) that require more rigorous justification. Additional evaluation, uncertainty analysis, and clarification of the parameterization framework are necessary before the manuscript is suitable for publication. I therefore recommend major revision.
Major Comments
- Physical realism of the 100% SOA mass yield assumption
The parameterization assumes complete conversion of the emitted surrogate VOC mass into SOA with a 100% yield. This is a very strong assumption and appears physically unrealistic. Although the authors cite Hodzic and Jimenez (2011), the implementation used here seems conceptually different from that study. In Hodzic and Jimenez (2011), the emitted surrogate VOC was effectively constrained such that only the SOA-forming fraction of organic vapors was represented, based on the relationship between SOA production and ΔCO (i.e., Emis(VOC)/Emis(CO) = SOA/ΔCO). In the present manuscript, however, the authors derive VOC emissions directly from observed VOC/CO emission ratios obtained from in situ measurements. These measured VOCs represent total VOC emissions and therefore cannot reasonably be assumed to convert entirely into SOA. As currently formulated, the approach appears to imply unrealistically large effective SOA yields. The manuscript therefore requires a much more rigorous justification of this assumption and a clearer explanation of how the surrogate VOC species are defined relative to actual SOA precursors. In addition, sensitivity simulations using lower and more realistic effective SOA yields, constrained by literature or chamber studies, would substantially strengthen the manuscript and help quantify the impacts on SOA, OA, and PM2.5 predictions.
- Lack of treatment of semivolatile partitioning
The proposed scheme effectively bypasses gas–particle partitioning physics and volatility evolution, which are central processes in SOA formation. The authors should discuss much more explicitly the limitations associated with omitting SOA thermodynamics and semivolatile partitioning processes. In particular, the manuscript should clarify how the dependence of SOA formation on aerosol mass loading is represented, whether SOA evaporation or repartitioning is possible within the parameterization, and whether any temperature dependence is included.
- Broader applicability of the proposed approach is unclear
The parameterization is constrained using VOC/CO ratios measured in Delhi during a single season (post-monsoon/winter). It is therefore unclear whether the proposed parameterization is applicable outside Delhi or under different seasons, especially during summer when photochemistry and biogenic SOA are stronger. The manuscript repeatedly suggests that the approach is suitable for operational applications over “highly polluted urban regions”; however, this broader applicability is not sufficiently demonstrated. The authors should discuss more explicitly the expected limitations of the parameterization to other regions, seasons, and chemical regimes, particularly given the strong dependence of VOC composition and SOA formation pathways on local emissions and meteorological conditions.
- Fire emission underestimation explanation is insufficiently demonstrated
The manuscript attributes the strong SOA underestimation during 13–19 November to missing fire detections under foggy conditions. While this explanation is plausible, it remains insufficiently demonstrated. The authors should provide additional supporting evidence, such as comparisons with independent fire products, aerosol optical depth (AOD) observations, CO measurements, or sensitivity simulations using scaled fire emissions.
- Comparison with MOSAIC is incomplete
The comparison with MOZART–MOSAIC is interesting but remains somewhat superficial. The authors compare only bulk SOA metrics (e.g., mean concentration, RMSE, and NMB), while important aspects such as diurnal variability, spatial distributions, and OA composition are not discussed. The manuscript would benefit from a more detailed diagnostic comparison to better demonstrate to what extent MOZCART can reproduce the performance of MOZART–MOSAIC despite its much simpler representation of SOA physics and chemistry.
- Clarification needed on AMS size range and comparison with PM2.5
The manuscript states that SOA and OA observations were derived from HR-ToF-AMS measurements of non-refractory PM2.5. However, standard Aerodyne AMS/HR-ToF-AMS instruments typically measure non-refractory submicron aerosol (NR-PM1). This discrepancy is important because the model evaluation compares modeled SOA/OA in PM2.5 with AMS-derived OA/SOA. The authors should verify whether their analysis involves a size-range mismatch and, if necessary, revise the comparison accordingly. If such correction is not possible, the manuscript should explicitly discuss how this mismatch may introduce an additional source of uncertainty in the model evaluation and interpretation of the results.
- Diurnal cycle mismatch deserves deeper analysis
The model peak occurs ~3 hours earlier than observations. The explanation is brief and speculative. The authors should analyze OH diurnal cycle, boundary-layer evolution, transport timing, and possibly nighttime chemistry contributions.
- Missing comparison against inorganic aerosol biases
Since simulated PM2.5 improves substantially after adding SOA, it would be useful to know how much of the remaining PM bias is due to inorganic aerosol. A PM2.5 composition evaluation would be useful.
Minor Comments
- language issues, typos, and formatting inconsistencies
Examples include:
- line 281: “practical phase” → “particle phase”
- line 476: “other oxidant like ozone” → “other oxidants such as ozone”
- line 477: “with in” → “within”
- line 520: “fogy conditions” → “foggy conditions”
- inconsistent spacing around units,
- lines 275, 438, 531, Tables 2-3: inconsistent use of µg/m3 vs µg m⁻³,
- inconsistent notation for OH radicals,
- duplicated references (e.g., Cubison et al. 2011 appears twice; DeCarlo et al. 2010 appears twice).
- Figure readability
Several figures are difficult to read:
- labels are too small,
- color contrast is weak,
- time-series are cluttered.
Figures 2–5 especially need larger fonts and clearer legends.
- Conclusions
The conclusion that the scheme provides an “optimal balance” may be overstated given the strong simplifying assumptions used, the lack of seasonal and spatial evaluation, and the limited uncertainty analysis.
Citation: https://doi.org/10.5194/egusphere-2026-1302-RC3
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General comments
This is a very narrow-focused study which only looks over one city in India, and only for one month of one particular year. This is very limited both for a comprehensive model evaluation (39 stations only in Delhi, while the whole Indian subcontinent was simulated) and the relevance to the journal itself, which clearly states in its aims and scope statement “Articles should have important and clearly argued implications for our understanding of the state and behaviour of the atmosphere and climate or present substantial new insights into the atmosphere's role in other parts of the Earth system. Articles with a local focus must clearly explain how the results extend and compare with current knowledge” (https://www.atmospheric-chemistry-and-physics.net/about/aims_and_scope.html).
Beyond relevance, the manuscript is weak both in terms of model development not being novel and ignoring important SOA-related processes, and by a weak model evaluation. My recommendation is to reject the manuscript.
Specific comments
Lines 67-74: Both the two-product model and VBS scheme follow the equilibrium assumptions of Pankow (1994), the difference is that in the two-product model there are effectively two volatility bins and OA mass is not transported from one to the other, while in the VBS there are more than two volatility bins, they are equally-spaced in the volatility space, and there is mass transport from one volatility bin to the other(s) via chemical processing.
Lines 128-130 and line 200: It is my understanding that SOA is implicitly represented in GOCART, even early versions of it, by simply assigning some OA source from biogenic volatile organic compounds (terpenes and maybe even isoprene). Yes, this is not an explicit SOA formation via equilibrium partitioning, but it is SOA formation nevertheless. Is this a capability that has been removed from MOZCART as used in AIRWISE? This is also relevant when presenting results in e.g. figure 3, do you literally mean “without SOA”? Because if indeed there is no SOA at all, then having lower results is only natural.
SOA parameterization: The approach of linking SOA to VOC and CO is over a decade old, and is very sensitive to the source terms used. It is not shown in the manuscript, but the simulations hold the data that can prove or disprove whether this parameterization is applicable elsewhere, or even in Delhi at other seasons and/or years. The authors should had made comparisons across India, in more urban areas as well as rural and remote areas. As a matter of fact, since the Hodzic and Jimenez (2011) work and its derivatives several new processes have been identified as critical to SOA, like photolysis (also studied by Hodzic), oligomerization, and phase state, which make the presence of a complicated mechanism rather than a simple one like the one presented here necessary. On top of that, such an approach completely ignores the temperature dependence of partitioning which forms SOA higher in the atmosphere, as demonstrated by measurements in the Amazon following deep convection.
Lines 295-296 and figure 2: The authors state “reasonably captures the observed variability”, but the black (measurements) and blue (model) lines differ by a factor of 3 for most of the period. What am I missing here? The discussion that follows simply cherry-picks dates and makes qualitative statements instead of doing a proper statistical analysis. I do acknowledge table 2, which says e.g. -45.8 % normalized mean bias. This is nowhere near “reasonably captures”.