Shen et al. investigate oxidative aging and gas–particle partitioning of cooking emissions using a Go:PAM flow reactor coupled with FIGAERO-CIMS (and supporting measurements). The manuscript argues that secondary organic aerosol (SOA) formation is driven primarily by nucleation/condensation of gas-phase oxidation products rather than by oxidative aging of primary aerosol. The authors further interpret the evolution of composition and volatility using a 2-D VBS framework and Positive Matrix Factorization (PMF), and they propose that smaller molecules approach equilibrium partitioning while larger molecules show non-equilibrium behavior that may reflect kinetic limitations.

The topic is potentially important. Cooking is increasingly recognized as a major contributor to urban primary emissions and to indoor particulate matter exposure, and detailed chemical characterization of cooking-related oxidation and partitioning can be valuable for both air quality and exposure studies.

However, in its current form the manuscript has substantial issues in analysis and presentation that prevent a rigorous evaluation of the main conclusions. My primary concerns center on the PMF approach/interpretation and the strength of several mechanistic statements. For these reasons, I do not think the manuscript is ready for publication in ACP without major re-analysis and restructuring, and I recommend rejection with encouragement to resubmit after substantial revision.

Major comments

1) Joint PMF on gas- and particle-phase signals requires stronger justification and validation.

The manuscript applies PMF to a combined dataset that includes both gas-phase signals and particle-phase thermal-desorption signals from FIGAERO. While a joint analysis can be feasible in some contexts, it requires clear justification and evidence that the solution reflects chemical/process factors rather than differences in measurement mode, time resolution, and uncertainty structure (real-time inlet vs. integrated filter collection + desorption). As presented, the manuscript does not provide sufficient validation that combining the two phases in a single PMF run yields physically meaningful factors. At minimum, the authors should demonstrate robustness (e.g., compare solutions from gas-only, particle-only, and combined analyses, and show whether the main conclusions are consistent).

2) The PMF results are presented in an overly descriptive manner, making the factor interpretation difficult to follow and limiting scientific insight.

Section 3.3 reports 13 factors and discusses their dominant ions/tracer-like species, but the factors are not assigned intuitive labels (source/process-oriented) and the narrative does not clearly articulate what each factor represents in a way that readers can track across the manuscript. As a result, it is difficult to understand why resolving these factors is important, how they connect to the SOA formation stages, and what new chemistry/mechanistic insight is gained beyond listing factor constituents. The structure of Section 3.3 also makes the discussion hard to follow; additional organization (e.g., subheadings and grouping factors by interpretation) would greatly improve clarity.

3) Mechanistic attribution of non-equilibrium partitioning to particle-phase diffusion / mass-transfer limitations is overstated relative to the evidence shown.

The abstract and conclusions present particle-phase diffusion/mass-transfer limitation as a key explanation for kinetic limitations in gas–particle partitioning of larger molecules. In the main text (Section 3.4), this appears to be one proposed explanation among others rather than a demonstrated mechanism. The manuscript does not provide quantitative constraints (e.g., phase state/viscosity proxies, diffusion coefficients or mixing timescales, uptake/accommodation considerations, sensitivity analyses) that would allow the reader to evaluate whether diffusion or mass-transfer limitations are sufficient to explain the observed deviations. Without such evidence, the current wording reads as a conclusion stronger than what is actually supported, and should be reconsidered.

Additional major comments / requests for clarification

1. VOCUS-PTR quantification: Please clarify whether and how fragmentation effects and compound-dependent sensitivities were handled for VOCUS-PTR quantification, especially for oxygenated oxidation products. This affects interpretation of precursor decay and product formation.
2. FIGAERO desorption completeness and background handling: Please clarify whether the authors verified complete desorption under the chosen thermal program for the expected aerosol loadings from cooking emissions (e.g., checks for residual signal, extended desorption tests). Also clarify how background/blank cycles were treated during the experiment and how that influenced the PMF input matrix and uncertainty estimates.
3. Use of “non-targeted” framing: The manuscript frequently frames the approach as non-targeted, yet much of the PMF interpretation relies on identification and discussion of specific tracer-like compounds. If the intent is truly non-targeted pattern extraction, more emphasis on bulk/ensemble descriptors (e.g., distributions in carbon number, oxidation state, volatility bins) and how these evolve by factor would be expected, in addition to listing specific ions.
4. Volatility in the 2-D VBS framework: Please clarify the volatility assignment strategy used in the main analysis. The manuscript states that saturation vapor concentration is estimated from elemental composition using an empirical parameterization, but FIGAERO also provides desorption-temperature information that is commonly used to infer volatility. If both approaches are used, their roles and consistency should be clearly described, and provide solid reason why Li et al method is used in 2-D VBS scheme instead of experimentally obtained C* data from FIGAERO.
5. Figure 1 / Section 3.1 clarity: In Section 3.1 and Figure 1, the evidence for new particle formation and condensational growth should be apparent from the increase in number concentration and the evolution of the size distribution. However, I found the current discussion somewhat difficult to follow and potentially internally inconsistent across panels. Specifically, if Figure 1a–b represent the primary aerosol size/mass distributions from cooking, I would expect these to closely resemble the lowest-OH-exposure cases shown in Figure 1c–d (i.e., near-zero oxidation). As presented, it is not clear to me how the “primary” distributions in 1a–b relate to the baseline conditions in 1c–d, or how the transition from primary to secondary distributions is defined in the plotting and analysis. Please clarify (i) what dataset/conditions are used for the “primary” panels, (ii) what OH-exposure case corresponds to the unoxidized baseline in 1c–d, and (iii) how the authors separate primary vs secondary modes across the figure.
6. Temporal evolution evidence for multi-generation products: Several statements about multi-generation oxidation products and their volatility class (IVOC/SVOC) would be strengthened by clearer presentation of temporal evolution (or oxidation-age-resolved) behavior of representative compound classes and/or factor contributions.
7. Nucleation mechanism vs. volatility class: The manuscript emphasizes growth in IVOC/SVOC material in the 2-D VBS framework. Please reconcile this with expectations for new particle formation pathways (often associated with low-volatility/ELVOC material), or clarify the nucleation/condensation mechanism implied by the observations.
8. Presentation and internal consistency (figures): The figures are often difficult to interpret quickly (labels/fonts/organization), and some figure citations appear inconsistent with the figure numbering/labels. Please ensure that all figure references in the text match the correct figures (including the Supplement), and revise figure labeling for readability.

This manuscript investigates the chemical evolution and gas-particle partitioning behavior of cooking-emitted organic aerosols using PAM flow-tube oxidation combined with FIGAERO-CIMS measurements and a 2-D volatility basis set framework. The authors aim to elucidate the compositional evolution and volatility distribution of oxidation products and demonstrate that non-equilibrium partitioning plays a dominant role in cooking-related SOA formation.

The topic is timely and relevant. Cooking emissions have increasingly been recognized as an important urban source of organic aerosols, and their oxidation chemistry and SOA formation mechanisms remain insufficiently understood. The combination of high-resolution FIGAERO-CIMS measurements, PMF-based non-targeted analysis, and volatility characterization provides potentially valuable insights into the evolution of cooking aerosols. The manuscript presents a large dataset and attempts to connect molecular composition with gas-particle partitioning behavior.

Overall, the study has the potential to contribute to the understanding of cooking-derived SOA and its kinetic limitations. However, several aspects of the manuscript require clarification and improvement before it can be considered for publication, as outlined below.

1. A central conclusion of the manuscript is that gas-particle partitioning of cooking-derived SOA deviates significantly from equilibrium due to diffusion limitations. However, the evidence presented for this claim is not entirely convincing. Several alternative explanations should be discussed more thoroughly, including uncertainties in FIGAERO-CIMS quantification, potential thermal decomposition artifacts during desorption, uncertainties in vapor pressure estimation, and limitations associated with the assumption of ideal activity coefficients in the equilibrium calculations. In particular, the comparison of partitioning coefficients relies heavily on estimated vapor pressures and assumed particle composition. Moreover, FIGAERO thermograms are known to produce fragmentation or rearrangement products, which may bias the inferred volatility and therefore affect the interpretation of partitioning behavior.
2. The experiments rely on PAM reactor oxidation with OH exposure up to ~1.8×10¹⁰ cm⁻³ s, corresponding to several hours to days of atmospheric aging. However, PAM reactors can introduce well-known artifacts: unrealistically high oxidant concentrations, secondary photolysis, altered radical chemistry, and enhanced fragmentation. The manuscript should clarify whether artifacts such as OH suppression and RO₂ chemistry differences were considered, and how the chosen oxidation conditions compare to typical indoor or urban atmospheric environments. In addition, cooking emissions are often influenced by NOx chemistry, which is largely absent here due to the use of pure nitrogen carrier gas. The implications of this experimental design for real-world cooking emissions should be discussed more carefully.
3. The authors note that iodide-CIMS detection may underestimate low-oxygenated or nonpolar species, such as long-chain hydrocarbons and fatty acids. This limitation could strongly influence the conclusions. For example, the reported small molecular size of primary aerosols and the inferred dominance of S/IVOCs may partly reflect instrumental detection bias. The manuscript should clearly discuss the detection efficiency of iodide-CIMS for cooking emissions, potential missing compound classes, and the implications for interpreting 2-D VBS distributions.
4. The PMF analysis identifies 13 factors representing volatile, semi-volatile, and low-volatility species. However, the physical interpretation of these factors appears somewhat speculative. For example, the assignment of factors to specific oxidation generations, the identification of fatty-acid cleavage products, and the interpretation of thermogram-derived volatility should be supported by stronger evidence. The authors should clarify how the optimal number of factors was determined, assess the robustness of the results with respect to changes in PMF configuration, and discuss whether the identified factors are chemically meaningful beyond statistical separation.
5. The partitioning analysis presented in Figure 4 compares experimental Kp values with equilibrium predictions. However, the methodology used to derive Kp from the FIGAERO data is complex, and the assumptions underlying the equilibrium calculations are not clearly described in the main text. Key parameters, such as the particle-phase molecular weight, organic mass concentration, and activity coefficients, should be explicitly stated. At present, much of the derivation is only described in the Supplement, which reduces clarity and makes it difficult for readers to fully assess the analysis.
6. Trace amounts of sulfur appear in the reported elemental compositions, but the manuscript does not discuss their origin. Since sulfur-containing compounds in cooking emissions are often associated with ingredients such as garlic or onions, clarification is needed. However, the experiments appear to involve heating corn oil only, without food ingredients. The authors should therefore explain whether the detected sulfur species originate from cooking emissions, background contamination, or uncertainties in molecular formula assignment.
7. Several details should be clarified: the exact composition of the cooking emissions (oil only vs food ingredients), repeatability of the experiments, and the number of experimental replicates. Currently, only corn oil heating at 120-130 °C is described. This may not represent typical cooking conditions.
8. Figures: The font size in several figures is too small and should be enlarged for readability (e.g., Figure 1(e)). In addition, the subpanel label “(e)” is not clearly marked in the figure and should be added to match the caption.