I very much appreciate the motivation behind this paper and think that the introduction reads quite nicely. However, the paper only contains 2 main text figures, which I do think is insufficiently short to tell a compelling mechanistic story as the authors are intending to do per the discussion. While I certainly see value in this experiment, I do not think the paper shows enough as written – to me, it reads as an introduction to a list of hypotheses instead of actually a demonstration mechanism, and the discussion/conclusion emphasizes those hypotheses over analysis of the data in hand. I think follow up experimentation/laboratory analyses on these reactors could be extremely beneficial to help support the ideas that are put forth in the discussion, to strengthen the merits of the study on its own accord. The bones of a good experimental paper are here, but as it currently stands, I do not think there is sufficient data or analysis to warrant publication currently.

Specific comments:

Introduction: I think this section reads very well!

Methods:

• In section 2.1, what is the rationale for supplementing your sediment with extra carbon? Further, why were leaves from another site used to do so? Are these standard practice for sediment/pond water incubation, or are your sediments naturally too low carbon to see a strong effect? Please explain and justify the method here more for clarity.
• Looking at table 1, your measured PVP concentrations are all fairly off from your expected. Nothing is far off enough to likely affect your experiment or matter for your conclusions since you are within the right order of magnitude, but please comment on the discrepancy in manuscript somewhere (i.e. where do you think the error is coming from).
• Section 2.3, you only cite flushing the headspace of your incubations for 30S and say this will generate anoxic conditions. These methods are insufficient for producing true anoxia – the oxygen in the headspace may be displaced, but the pond water and sediment are not noted as being collected/handled in an anaerobic fashion. Did you sparge the water/sediment slurry with nitrogen as well, or are you depending on oxygen respiring organisms to deplete the oxygen present in the bottles and hope the methanogens persist until then? Please explain the methods here more.
• Section 2.4 confused me some – did you do RNA extraction followed by 16S rRNA sequencing of the cDNA produced from that, versus typical methods of 16S sequencing based on just DNA? This is not typically done for 16S analysis, but I think is quite a cool way to do this if the choice was to effectively get an activity proxy for cheaper than MetaT sequencing. I think the rationale for the way you did this needs clarifying, but also that this method you chose is quite cool and is something you could upsell and discuss more!
• Section 2.6 is quite dense, and honestly hard to read as a non-expert in the equations presented - Is there anything that could be done to help simplify this?
• The explanation of the phases of methanogenesis is also unclear to me – do you mean these are typical phases in a closed system? Same uncertainty in line 211.

Results:

• Figure 1 – it’s not clear to me what the inflection point is. It is somewhat defined in section 2.6, but in a technically challenging fashion for the average reader to understand. I think a more casual definition in the results would help readability here.
• Figure 1 – this isn’t clearly discussed, but the 0.5 mg per L treatment seems to buck the otherwise linear response trend in your data in 2 of 3 metrics measured. I think this for sure needs discussion/analysis in the manuscript.
• Typo on line 230 – “ASVs o average”
• Table 2 – I don’t understand the two groups of taxa as phrased, since Euryarchaeota are The grouping/organization needs renaming here for sake of accuracy and clarity.
• I think Figure S6 would be a reasonable main text figure instead of a supplemental – that is data I wanted to see to be able to understand/assess Figure 2, so it is definitely important data.

Discussion

• As an overall comment, I don’t think there is much analysis of your own data here, versus review of literature. I think this paper really would benefit from more specific analysis of the figures before the theorizing on mechanism comes in.
• Line 244: how meaningful is a 2-hour difference in reaching this inflection point? Is this an ecologically significant difference?
• Lines 244-245, also stated above, the 0.5 mg per L treatment does not follow the trend you are purporting in the paper of a maybe linear increase in the metrics with PVP dosing, so I think that really needs to be discussed.
• Lines 249-251 – I am not following the basis of this assumption. Do you have organisms in your community that are specifically known to produce EPS in response to plastic? Is this a taxa-specific response? The theorizing here feels too general to me.
• As with the EPS idea, the discussion of TEAs and iron feels unsubstantiated to me in the current manuscript. Could you do a ferrozine assay or something to measure iron in the incubations to support this idea for your own experiment? Or if you do not have any more sample material, could you at least look for iron-cycling taxa in your data? Is iron relevant to your specific sediments? There is a lot of discussion of iron metabolism specifically here without clear linkage to your data and material.
• Line 283 – please change kingdom to phylum
• You talk about the need for explicit mechanism testing in a follow up paper, but I don’t quite understand why that data is lacking from this manuscript e.g. I think this current work needs more data to be able to say much to most of what you say in the discussion section. I fully understand that there might not be stored/extra experimental material to do more chemical analysis on to look for iron/TEAs, EPS production, etc, but at least the microbial data in hand could be used to do more to get at addressing the ideas brought up in the paper.

The manuscript evaluates the methane production potential during a 56-day anoxic incubation of sediments after amendment of polyvinylpyrrolidone (PVP). PVP was used as a representative of synthetic hydrophilic polymers (SHP), which are increasingly used and released into the environment. Results indicated the presence of PVP increase the CH4 production potential and influences the microbial community.

I am less qualified to evaluate technical molecular biology details and the microbial community aspects, so this review focuses on the other parts of the manuscript.

I find the focus on SHP interesting, and in general found this study well-executed and the manuscript well-written. However, I have some questions that require clarifications.

How much SHP/PVP can be expected to reach sediments? Why are sediments a key environment to evaluated effects of SHP/PVP in?

L55. How can PVP be chemically stable if it has clear effects on sediment carbon cycling in the experiment?

Please express sediment carbon content including the leaf powder addition and PVP with comparable units so it is possible to relate all components with the sediment carbon budget and the CH4 formation.

L77-78: Why are wastewater treatment plants increasing the PVP concentrations 8-70-fold compared to sewage water?

L81. pH adjustment: Please tell more about this pH sensitivity. How sensitive would PVP degradation or other experimental results be to pH? What are the implications of this for the results? How valid are the results in situ t other pH levels?

L95-97 and Table1: It seems the two lowest levels of PVP amendment (0,5 and 50 mg/L) are below LOQ  (70 mg/L), and initial measurements at 50 and 5000 mg/L were <80% of the amendments. Please explain why there is such a large discrepancy. How robust is the method? What was the background PVP level in the original sediment?

Eq 1. The final addition of xe is unclear. What does this mean? Why is it needed? Perhaps I misunderstand, but in later equations the number of moles in the headspace and the water is calculated separately and summed to derive the total amount, and that should take care of all partitioning between headspace and water, and a mole fraction correction as expressed in Eq1 seems strange?

Results and Fig. 1: So, over a PVP-addition range from 0 to 5000, the CH4 production potential increase 20% (1.2-fold). 30% (approx.) of this increase occur happen when the PVP addition increased from 0 to 0.5. The rest happens when increasing PVP 50 000-fold. Accordingly, although the results are significant, the response on CH4 is rather modest in relation to the very large change in PVP concentrations. Please discuss this and what it could mean in the manuscript. Is it possible that this effect is linked to something else than PVP given the experimental setup, or can that be excluded? Are that any alternative interpretations of the results?