the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
| 23 Apr 2026
Seaweed and coastal plant biomass-stimulated methane emissions driven by methylated compound content
Abstract. Methane emissions from coastal sediments are increasingly influenced by ecological change, including eutrophication-driven seaweed blooms and efforts to restore coastal vegetation. Yet the pathways and variability of methane production in these environments remain poorly constrained. Here, we compared methane production from three seaweeds (Ulva, red filamentous algae, and kelp) and three coastal plants (mangrove leaves, saltmarsh plants, and seagrass) in sands from Port Phillip Bay, Australia. To identify potential predictive precursors, we quantified key methylated osmolytes (dimethyl sulfoniopropionate (DMSP), choline, trimethylamine (TMA), trimethylamine N-oxide (TMAO)), that serve as methanogenic substrates. Methane production from seaweeds was strongly correlated with osmolyte content, whereas coastal plants, particularly mangrove leaves, stimulated methane production despite low osmolyte levels, likely via decomposition pathways generating methanol. These findings broaden the understanding of organic matter sources fueling methanogenesis in coastal sediments and highlight an overlooked contribution of both seaweeds and plants to coastal methane cycling.
Competing interests: At least one of the (co-)authors is a member of the editorial board of Biogeosciences.
Publisher's note: Copernicus Publications remains neutral with regard to jurisdictional claims made in the text, published maps, institutional affiliations, or any other geographical representation in this paper. While Copernicus Publications makes every effort to include appropriate place names, the final responsibility lies with the authors. Views expressed in the text are those of the authors and do not necessarily reflect the views of the publisher.- Preprint
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Status: open (until 08 Jun 2026)
- RC1: 'Comment on egusphere-2026-2113', Anonymous Referee #1, 21 May 2026 reply
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RC2: 'Comment on egusphere-2026-2113', Anonymous Referee #2, 31 May 2026
reply
The manuscript by Hall et al. investigates how different types of marine plant and seaweed biomass influence methane production in sandy sediments collected from a bay in Australia. The authors incubated sandy sediments with biomass from seaweeds and coastal vegetation, including mangroves, seagrasses, and saltmarsh plants, and monitored methane concentrations over time. In addition, they quantified the concentrations of choline, DMSP, TMAO, and TMA in the various biomass types. Because these compounds are known methane precursors, the authors multiplied their measured concentrations by the number of methyl groups contained in each compound to estimate their potential contribution to total methane production.
The most interesting and novel finding of the study is the variation in methane production among the different biomass additions. In particular, Ulva and mangrove biomass stimulated higher methane production than the other biomass types. These findings raise important questions about how future shifts in the abundance and distribution of marine plants and seaweeds may influence methane emissions under ongoing environmental change.
In my opinion, the study is an important addition to the growing literature on the importance and drivers of methylotrophic methanogenesis in coastal sediments. However I identified a couple of concerns and can not recommend it for publication in its current form.
Main comments:
1. Calculating sum of methyl groups
I have some concerns about the way the methane production potential of the different plant types was estimated based on the number of methyl groups of the quantified osmolytes. First, the authors appear to assume that all methyl groups of a given osmolyte are available for methanogenesis and can therefore be reduced to methane. However, it is unclear what electron donor would support the reduction of all methyl groups. Is it hydrogen? I actually think that electron are rather derived from the oxidation of additional methyl groups to CO2, in which case not all methyl groups are in fact reduced. I think this needs to be taken into account and may require revisions of some of the conclusions of this study.
Second, how confident are the authors that indeed all methylated compounds that could serve as methanogenic substrates have been quantified? One notable omission is glycine betaine, which has been identified as a direct substrate for methanogenesis. The exclusion of glycine betaine and its breakdown products could influence the estimates of the relative contributions of the measured osmolytes to methane production.
2. Role of pectin and methanol
In mangrove incubations, the amount of methane produced could not be fully explained by the amount of osmolyte quantified and the authors instead link this methane production to methanol which forms during the breakdown of pectin. However, there is no actual data presented that would support these statements, even though methanol has apparently been measured. I think either data on methanol measurements have to be added or the conclusions about the role of methanol has to be revisited.
3. Figure 1
I think Figure 1, in its current form, is misleading. Figure 1 presents a universal pathway of methane production in coastal sediment that is more like a summary of the existing literature or shows assumptions that are not supported, like the role of pectin. The figure actually implies that there is a universal pathway by which methane is formed in vegetated sediments irrespective of the type of vegetation which seems to contradict the findings of this study. The novel findings of this study, the comparison of different biomass types, is not shown at all. In my opinion, this figure needs to be substantially revised or removed.
4. Results part
I think the results part is very short and misses some key results. I suggest to include data on the absolute osmolyte content of the different biomass types as well as any data available from the methanol analyses.
Line-specific comment:
Line 20: What does “despite low osmolyte levels” refer to? If I look at your dataset 2, mangroves, seagrasses and saltmarshes seem to have the highest levels of choline and trimethylamine. Please clarify.
Line 96: Was this done under anoxic conditions? If not, could it be that exposure of the sediments to oxygen could have inhibited the methanogens which could have led to the lag phase at the beginning of the incubation?
Line 98: Sentence is incomplete
Line 103: How much biomass was added for incubations with plant material?
Line 111: Please include data on methanol analyses here and throughout the manuscript.
Line 112: Why was the experimental setup for the methanol determination different than for the other slurry incubations (less sand and seawater, more plant biomass)?
Line 122: Was the collected gas sample injected into the 3 ml exetainer with or without releasing the overpressure?
Line 145: It is not clear what “all measured concentrations fell within the calibration range” refers to. In Table 1 LOD and LOQ are shown for four measured compounds but it is not stated what LOD and LOQ were used for in the interpretation of the data? Were all measured compounds above the LOQ for all measured samples? If so, then why are some of the compounds reported as zero in dataset 2? I think this needs clarification. Also, please add units of data shown in datasets 1 and 2.
Line 160: How did you get to the dry weight of added biomass in the slurries?
Line 165: Please see my main comment above about the number of methyl groups available to methanogens.
Line 189: the authors state that DMSP was the dominant substrate, as close to 100% of methyl groups were converted to methane. Looking at Figure 3, all seaweed types show that methane production stopped after around 200 hours. Does this mean that by that time all DMSP had been converted to methane? If so, I find it surprising that the same was observed for the control experiment that contained high (80µM) DMS and was probably not limiting.
Line 235: Terms seaweeds and marine plants are mixed here
Line 265: Without presenting any data on methanol this statement has to be removed.
Citation: https://doi.org/10.5194/egusphere-2026-2113-RC2
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- 1
The manuscript by Hall et al., performed sediment slurry incubations, headspace methane determinations, and metabolomic analysis to show potential methylotrophic methanogenesis in sandy sediments derived from osmolytes commonly found in seaweeds (e.g., Ulva) and coastal plants (e.g., mangroves). They found that degradation of kelp and red filamentous developed low concentrations of methane. Whereas incubations with degrading Ulva biomass led to significant methane development. I believe the work is important, and relevant tot eh scope of Biogeosciences, but as it stands the manuscript has several that must be addressed before recommendation for acceptance/publication.
Major comments:
1). The paper needs more citations that are critical, specifically papers that investigate the production of osmolytes and their role in methane production See publications from Wang and Lee, 1994 and 1993 and seminal studies from Aharon Oren.
2). Methanol was a suspected substrate for methanogenesis, why did the incubations not include a methanol control and why was Pectin (the precursor to methanol) not analyzed in any of the host organic matter and during the incubations? Given that the results apparently found little no methanol and with no data to show, it may be worth considering getting rid of that text all together.
3). The results are not well described and could be organized better, specifically regarding methanol, which seems to be lacking.
4). The discussion, unfortunately, is the weakest part of the manuscript. Particularly, the interpretations of the data are either contradictory or have no teeth because no data shown (i.e., methanol trends). Moreover, the authors could elaborate more on the broader impacts and significance of the data and interpretations of the study throughout the discussion. I have identified areas that need attention in the in-line comments below. Lastly, the discussion ends rather abruptly. I suggest the authors either add a concluding paragraph or a conclusions chapter that summarizes their findings.
In-line comments:
L32: There are many other papers that show methylotrophic methanogenesis activity in coastal environments that you can include such as Xiao et al., 2017; Maltby et al., 2016; Zhuang et al., 2026; Krause et al., 2021 and 2025 and probably several others.
L50: I would suggest adding citing papers from Oren and Lee and Wang who did some seminal work on production of methylated substrates in coastal environments including coastal wetlands.
L95-96: How does sieving and homogenizing the 0-5 cm layer provide a seed population of methanogens? Were methanogens added to the sediment? Needs clarification.
L98: Incomplete sentence…
L100: In this section the authors prepared sediment slurries with different ratios of sediment slurry to kelp biomass. Is there a reason why these ratios are so different? For example, the kelp biomass to sediment is <1% but there is 10% mangrove leaves to sediment. There could be one sentence here to explain why these proportions were chosen. Additionally, there are differences in incubation times for each set of slurries, but no clear explanation as to why.
L104-105: I think this sentence could be split into two for clarity.
L106: How long were samples purged with argon for?
L107: If you did do artificial day/night cycles then you need to elaborate more (e.g., duration in the light vs. at night and by what light source).
L111-117: Were controls prepared for this incubation?
L113-115: Spell out “5”. Numbers in the beginning of sentences should be spelled out. This sentence does not read well; I suggest reorganizing it for clarity.
L121: Are these the same time points listed in the previous section?
L128-132: Issues with this sentence. Spell out “20” if it’s the beginning of the sentence. The long parenthetical could be a separate sentence. There are several grammatical errors that make the sentence hard to understand. I recommend reorganizing for clarity.
L175-176: Citation? What is the theoretical methane production potential based on? Is it based on how many moles of TMA and DMS that were added? Needs clarification.
L201-202: I think this sentence is rather vague and just breezes by some important details in the data. The authors can expand a little more on this result description because although see the DMSP being dominant in the Ulva, one could also see the dominance of Choline in the Mangrove samples. I think 1 or 2 more sentences to cover these important trends would make it stronger.
L205: I suggest that the authors be careful with using the word “plants” in their manuscript. Technically, seaweed is not plants, they are algae. I think in colloquial conversations “plants” can be used and understood to mean kelp and other seaweeds but in peer-review journals one should be careful.
L215: Citation? Is there literature on how DMSP supports methanogenesis not only by providing the methyl group but also the nutrients (i.e., P) for metabolic activity?
L225: Can the authors elaborate on what “other plant components” are specifically? Isnt it possible that after that 7-10 days the most labile osmolytes are consumed and the system reaches a steady-state or has a tough time breaking down the more recalcitrant organic matter from the seaweed to further produce methane production? What data supports the claim, since there doesn’t seem to be a tracking of osmolyte concentration in the batch incubations to suggest exhaustion?
L230-232: I agree that methanogen abundance probably starts low (do you have data to support that?) but two other things need to be considered 1) the system needs to be fully anoxic, which even with the procedure may still have small concentrations; 2) I also think that the algal and plant biomass added to the system still has intact cell structures that contain the osmolytes which need time to break down and release the osmolytes. This would be easy to tell if osmolyte concentrations during the study were monitored overtime. Additionally, I can see how methanogenesis in this case is a transient phenomenon, but can the authors elaborate more on why that might be and the significance of this observation. If methanogenesis is short lived from these organic matter sources, then why should we care?
L240-245: Your data in figure 3A does not really suggest Red Filamentous Algae to be a potent contributor of methane. Only one location saw some methane development but was more than half less than the Ulva condition. Maybe expand here a bit as to why Red Algae don’t contribute much methane perhaps Figure 4B has some suggestions. Moreover, this statements sort of contradict your previous section where methane production appears to be short lived. So why do we care in the context of this study if Ulva becomes more abundant with warming climate if methane production is short lived?
L245-247: I am not really sure what this statement is getting at? Are you trying to imply that Sargassum may lead to methane production when washed up on beaches? If so, I would expand a bit otherwise it doesn’t really fit well with the story.
L248: This section has no teeth since no methanol data was shown.