The manuscript by Lines et al. investigates the response of stream biofilm microbial communities to storm-event-driven pulses of dissolved organic carbon (DOC) in a sub-alpine peatland catchment. This is a relevant topic, given the projected increase in storm intensity under climate change and the critical role of biofilms in aquatic carbon cycling. The study employs a comprehensive multi-method approach that combines detailed hydrology, sophisticated DOC characterisation, and high-throughput sequencing of algal, bacterial, and fungal communities. The central finding – that biofilm community composition remained largely stable following short-term DOC pulses and was instead more strongly influenced by site-specific factors – is noteworthy and contributes a valuable perspective to the field. The manuscript is generally well-written, and the data appear robust. However, several points require clarification and further discussion to strengthen the interpretation of the results and the overall impact of the study before it can be considered for publication.

Major Comments

1. Temporal Resolution of Biofilm Sampling: Biofilms were sampled only “within 24 hours prior to zero storm time” and “12–16 days after each storm event.” This gap misses short-term (e.g., 1–7 days post-storm) community dynamics, which could reveal transient shifts that recover by 12–16 days. For example, if biofilms temporarily respond to DOC pulses but revert to pre-storm composition by the post-storm sampling, the current design would mischaracterise “stability” as absence of change rather than resilience. If retrospective sampling is not possible, discuss this limitation explicitly and propose future studies with intermediate time points (e.g., 3, 7 days post-storm) to capture potential short-term responses.
2. Interpretation of the PERMANOVA Results: The significant three-way interaction (Event × Site × Storm-time) is reported, but the subsequent analysis and discussion focus heavily on the overwhelming effect of 'Site'. The PERMANOVA model uses Type I (sequential) sums of squares, meaning the variance explained by 'Site' (entered first as a random factor?) is removed before testing the other factors. The authors should clarify the order of factors in the model and consider whether the significance of the three-way interaction is largely an artefact of the strong site effect, as they allude to. A more detailed presentation of the variance explained by each term (e.g., via a more complete table than S10) would be helpful. Furthermore, for the pairwise tests following the significant interaction, the use of Monte-Carlo p-values due to low permutation numbers should be explicitly stated in the main text methods, not just the supplement.
3. Linking DOC Change to Biofilm Function: The study expertly characterises DOC composition but does not link these changes to any functional response of the biofilms (e.g., metabolic activity, extracellular enzyme assays). The authors hypothesise that the biofilm matrix may buffer against change, but without concurrent data on microbial function or carbon utilisation, this remains speculative. Whilst a comprehensive functional analysis may be beyond the scope of this paper, the discussion on why the communities are stable (Section 4.2) would be strengthened by acknowledging this gap and suggesting that functional stability (or plasticity) could occur without compositional shifts. Are the observed communities functionally redundant?
4. Climate Change Implications: The manuscript concludes that biofilm stability “suggests that with the predicted changes in the frequency and intensity of storm events under a warming climate, these communities may be resilient” (p. 29). However, it does not address whether repeated storms (e.g., the three events between SE1 and SE2, p. 12) could exhaust resilience over time. For example, if each storm depletes EPS stores, successive pulses might eventually trigger community shifts. Discuss the limitations of extrapolating from two storms to long-term climate change, and propose future studies on the effects of repeated DOC pulses on biofilm resilience.

Minor Comments

1. Introduction: The introduction is comprehensive but could be more sharply focused. The link between DOC characteristics, bioavailability, and expected microbial community shifts could be articulated more directly early on to set a clearer hypothesis.
2. Methods (Section 2.7.1): The use of a correlation cut-off (r ≥ 0.7) to remove variables from the PCA is a valid approach to reduce multicollinearity. However, the choice of the cut-off is somewhat arbitrary. A brief justification for this threshold would be helpful. Furthermore, stating that DOC is "best represented by Electrical Conductivity" is an overinterpretation; it is correlated with, not a direct proxy for.
3. Discussion (Section 4.2): The argument that short water residency times limited community response is compelling. Could the authors provide a rough estimate of water travel times during peak flow vs. baseflow for their sites to quantitatively support this line of reasoning?
4. Language and Typography: The manuscript is well-written but would benefit from a final proofread for minor grammatical inconsistencies (e.g., consistent use of present/past tense). Ensure all acronyms are defined at first use.

I recommend major revisions.

Overall assessment

The authors present a very clear and well-structured study that includes an impressive array of streamwater chemistry and biofilm responses across entire storm events. Given the comprehensive characterisation of storm event carbon quantity and quality, and of biofilm community responses, this work makes and excellent contribution to the generally understudied topic of benthic responses to hydrological events. I therefore suggest only a few minor revisions (see below) before acceptance.

Detailed comments

109-110: How was storm event duration defined in more detail, i.e., which criteria were used to define the end of events? Note that SE1 would be classified as two storms with some commonly used criteria (e.g., returning to <100% baseflow).

138: Firstly, pH, EC, and DO are physicochemical parameters, not physical. Secondly, could the authors clarify what is meant by triplicate sampling of these parameters? I suspect that what the authors mean is that the water samples were collected in triplicates.

140: I can not find any DO results reported, what is the reason for this? Also, if not included in results it can be removed from the methods section.

146-147: When were subsampling and filtration carried out? This is important for assessing the quality of the subsequent analysis.

148-149: I suggest clarifying this as “Subsamples collected for optical characterisation of DOC by spectroscopic analysis”, to not confuse these with subsamples used for other DOC characterisation.

158: Could the authors provide more details for how planar projections were achieved?

168: Organic nitrogen detection (OND) was not included in the analysis, thus the method used is LC-OCD.

170: Correct to “HORIBA” in all further mentions.

208-212: Given that biofilm biomass and chl-a were expressed per area, was eventual differences in biofilm thickness in situ accounted for?

253: Suggest clarification as “Seven missing samples corresponded to an exclusion of 55 datapoints”

359: Responses in EC is technically not a salt pulse, it is a pulse of charged ions.

546-567: I fully agree that the shorter DOC exposure time, given limited storm durations but also short solute residence times, is a convincing reason for community composition stability. Previous studies that are discussed in this paragraph are appropriate in the way that they investigated effects of DOC concentration and quality on community composition, however, none of these studies have been carried out during storm events. Thus, the authors could consider to also discuss other studies that do include storm event responses, e.g., of whole-stream metabolism: https://doi.org/10.1029/2019WR025025, https://doi.org/10.5194/bg-19-1111-2022, https://doi.org/10.1029/2024JG008308.

595-600: The occurrence of scouring, and potentially also burial, may be more unambiguously interpreted from combined changes in chl-a content and biomass. Chl-a could more directly indicate scouring/deposition, circumventing confounding effects of detrital deposition in biomass changes.