Thank you for the suggested edits. Below we respond to each comment with our planned revisions. Our text is in bold font, while the reviewer's text is in normal font.

Reviewer 1:

General

As papers on river ecosystem functioning are booming, the exact meaning and the interrelation of different "ecosystem processes" are becoming a hot issue. The paper by Stegen et al. makes an interesting contribution to the field. They measured cotton-strip decomposition at 48 sites across the Yakima River Basin (YRB) and compared the results to a paper (Garayburu-Caruso et al., 2025), performed at the same sites, that measured whole-ecosystem and water-column respiration, and inferred sediment respiration. Stegen et al. found that cotton-strip decomposition is more tightly linked to total (whole-ecosystem) than to sediment respiration, an unexpected outcome. They also found, unsurprisingly, a very high variability in cotton decomposition across the YRB.

Overall, the paper makes a nice contribution to the field. The methods are sound, results interesting and the discussion mostly accurate. There are, however, some small issues that should be considered before publication.

Thank you for the encouraging remarks and for the suggested improvements. Below we detail our planned revisions based on your suggestions.

Specific comments

The title is a bit misleading. The paper shows point-scale organic matter decomposition to be more tightly linked to total than to sediment respiration but does not clearly address (or not in sufficient detail) the basin-scale connection between both processes. The authors should find a title that better reflects their findings.

The current title is: “Basin-scale connections between reach-scale sediment respiration and point-scale organic-matter decomposition.” We plan to edit this to: “Point scale organic matter decomposition in streambeds is weakly associated with reach-scale sediment respiration.”  

L15-16. Is "microbial-catalyzed" a correct expression? Better rewrite as "microbially-catalyzed" or as "microbe-catalyzed".

 We plan to edit to “microbe-catalyzed.”

L24-26. It is hard to imagine a mechanism for this relationship between cotton decomposition and whole-ecosystem (but not sediment) respiration.

We too were surprised by the result. We plan to further elaborate on our interpretation within the associated Results and Discussion section, as opposed to adding more interpretation to the Abstract.

L51. The accumulation or release of carbon is not a measure of heterotrophicity. A heterotrophic ecosystem is one that produces more organic carbon than it mineralizes, which is not exactly the same thing. Please, rephrase.

 The original version of the sentence was: “Streams are commonly net heterotrophic whereby they release more carbon than they accumulate (Battin et al., 2023; Bernhardt et al., 2022).”

We plan to revise it to: “Streams are commonly net heterotrophic, meaning they mineralize more organic matter–associated carbon than is fixed by in-stream primary production (Battin et al., 2023; Bernhardt et al., 2022).”

L88-96. Please, give more details about the Garayburu-Caruso paper. Explain the estimated length of the reaches for which whole-ecosystem respiration was calculated and whether this length could create autocorrelation issues between neighboring sites.

We plan to add text to the Methods section addressing these aspects of the data. In short, per Garayburu-Caruso et al. (2025), reach length likely varied across sites due to variation in oxygen turnover. Field sites were in separate reaches to help avoid spatial autocorrelation. 

L100-101. ERsed was calculated from the difference between ERtot and ERwc. This will, thus, include respiration in the hyporheos, on the sediment surface and by submerged plants, but also any non-respiratory process that consumes oxygen, such as oxydation of metals in upwelling groundwaters. The authors should be more cautious when linking oxygen consumption and respiration and specifically state that there can be multiple non-respiratory processes consuming oxygen across a basin. It would also be nice to see this issue in the discussion.

We plan to include caveat statements in the Methods and in the Discussion, per the reviewer’s suggestion. We will inform these caveat statements with stream metabolism literature as all stream metabolism research using single station dissolved oxygen sensors have the same caveats.

L106. Strips were deployed on the surface of the riverbed and covered with a brick. This makes them much more likely to correlate with processes occurring at the water column than if they had been deployed deeper into the sediments. Authors should at least discuss the effects of their methodological choice.

The sentence reads: “The cotton strips were deployed at the interface between water and sediments…” To more fully bring that methodological choice into the interpretations, we plan to add some additional discussion on this point in the relevant Results and Discussion subsection. For example, because the deployment was at the interface, the cotton strips were being impacted by processes in both the sediments and surface water. That may be a key reason that total ecosystem respiration (that includes respiration associated with sediments and surface water) was more strongly related to decomposition than were sediment or surface water respiration alone.

L113. 7th-order rivers can have very deep sections. The authors seem to have deployed all their strips on wadeable parts of the river. It would be good to at least give some caveats about this reflecting "true" decomposition across the river, and better to discuss how this could have affected results.

We plan to address this by including additional recognition that our decomposition estimates are point measurements and do not capture the full heterogeneity of decomposition rates across a given reach. We agree that this is important to emphasize so the reader has a clear understanding of the study’s limitations. We will include this in the last subsection of the Results and Discussion.

L116. The four replicated strips were deployed next to each other, which is very convenient to deploy and recover them, but not at all when we want to capture sediment decomposition rate of a reach that for whole-ecosystem respiration can be hundreds to thousends metres long. The literature has shown breakdown rates to differ markedly from consecutive riffles, even more so between riffles and pools, and even more between substrata deployed on the sediment, as is the case here, and in the sediment. This should be mentioned as a caveat on the methodology and discussed later on.

It is a valid point that the study design did not attempt to capture spatial variation within reaches. This is related to the comment immediately above as it has to do with spatial variation across any given reach. We will use the same approach, whereby we plan to include additional recognition that our decomposition estimates are point measurements and do not capture the full heterogeneity of decomposition rates across a given reach. We agree that this is important to emphasize so the reader has a clear understanding of the study’s limitations. We will include this in the last subsection of the Results and Discussion.

L139-146. It would be interesting to compute respiration in degree days also.

We agree that would be interesting and would parallel the degree day based estimation of decomposition. Currently, we’re unclear how to achieve this based on the existing data. That is, we are using respiration estimates from the Garayburu-Caruso et al. (2025) study and they do not provide respiration per degree day. They provide an average instantaneous respiration rate for the whole deployment period, which is different than the cumulative amount of decomposition that occurred during the deployment period. We will consider this more deeply and either include respiration normalized by degree days (if we deem this technically robust) along with associated interpretation, or we will provide one sentence calling out this idea as something to attempt in future efforts (if we deem this not technically robust).

L154. "....rates, a..." replace point by comma.

We plan to make this edit.

L169. The variation in decomposition rate is surprising given that data come from a single basin? Not so much. Benthic processes are extremely patchy. But this also draws the question whether 4 strips are enough to characterize the decomposition of a reach whose metabolism has been characterized by the open-channel method, which typically has a spatial extent of hundreds to thousands of metres.

As discussed above, our plan is to include more direct acknowledgement in the final subsection of the Results and Discussion of the fact that we did not estimate spatial variation in decomposition within each reach. We will also emphasize that this was done to enable decomposition estimation across reaches (i.e., there is an inherent tradeoff between among vs. within reach variation estimation). 

L173-174. Delete. Climatically diverse basins are interesting, but any other diversity factor (geologic, topographic, human...) can result in interesting information.

The original sentence read: “This emphasizes the value of climatically diverse watersheds like the YRB as useful testbeds to study variation in decomposition rates within single hydrologically connected basins.”

We plan to edit this to: “This emphasizes the value of environmentally diverse watersheds like the YRB as useful testbeds to study variation in decomposition rates within single hydrologically connected basins.”

L178-181. High decomposition rates in summer have been often reported. Nevertheless, it is unclear whether these derive from high temperatures, as even when correcting by degree days the decomposition tends to be higher in summer. It is also unclear these high rates are a consequence of slow flows, as slow flows can also reduce the exchange of nutrients etc. between water and OM, thus slowing decomposition. In fact, comparison between mesohabitats systematically show decomposition to be faster on riffles than on runs or pools. Therefore, the high summer decomposition rate more probably is a consequence of the longer time of stability since the last disrupting floods, which allows developing the biological communities, or the less diluted waters, which enhance nutrient concentration. Please, discuss in greater detail.

The sentence referred to is: “This shift towards faster rates and the wide range in rates may be because YRB rates were estimated in later summer, a time of year when decay processes are likely maximized due to relatively high temperatures and slow flows (Collier et al., 2013b; Mancuso et al., 2023).”

We believe the reviewer is asking us to elaborate on the potential effects of a long time-since-disturbance that could allow more robust biological community development. We plan to revise the sentence to something like: “This shift towards faster rates and the wide range in rates are likely due to several factors linked to rates being estimated in later summer with high temperatures, slow flows, and established biological communities due to several months since high-flow disturbances (Grimm and Fisher 1989; Collier et al., 2013b; Mancuso et al., 2023).”

L182-185. Not so surprising. This simply shows that in the YRB other factors (nutrients? sediment biota? fine sediment accumulation? toxics?) override the effects of temperature, what also has been reported in many papers.

The sentence referred to is: “These results are surprising given previously reported influences of temperature on particulate organic matter decomposition (Benbi et al., 2014; Griffiths and Tiegs, 2016).”

We plan to revise the sentence to something like: “These results are surprising given previously reported influences of temperature on particulate organic matter decomposition (Benbi et al., 2014; Griffiths and Tiegs, 2016), and likely reflect dominance of other influential factors such as nutrients (Rosemond et al. 2015).”

L215-217. I cannot agree. From the description it seems the strips were located on top of the sediments, and below one brick. This is not exactly hyporheic. Other authors have measured decomposition within the sediments and found it to greatly differ from that on the surface.

The sentence referred to is: “These results are surprising, in part, because the cotton strips were deployed within the shallow hyporheic zone (i.e., within the riverbed sediments).”

The result the sentence refers to is “...decay rates were most strongly connected to ERtot, less so with ERsed, and not at all with ERwc (Fig. 5).”

The deployment strategy was such that the brick was at the same level as the streambed such that cotton strips (below the brick) were a few cm into the streambed. Where exactly the hyporheic zone starts is ambiguous, which is why we write “...the shallow hyporheic zone (i.e., within the riverbed sediments).”

To avoid calling out the result as ‘surprising’ we plan to revise the sentence to something like: “To interpret these results, we note that cotton strips were deployed a few cm into the riverbed sediments, which we interpret conceptually as the shallow hyporheic zone.”

L220-228. Very speculative and will depend ultimately on the contribution of epilithon to the total sediment respiration, which can be highly variable depending on the extent and activity of the hyporheic zone.

The sentence referred to is: “We propose that if our deployment configuration was complemented with a simultaneous deployment that enabled growth of benthic algal biofilms on the cotton strips, the combined decomposition from both deployments would capture substantially more of the processes that contribute to ERsed.”

We plan to revise the sentence to something like: “We propose that if our deployment configuration was complemented with a simultaneous deployment that enabled growth of benthic algal biofilms on the cotton strips, the combined decomposition from both deployments could--in some systems--capture more of the processes that contribute to ERsed.”

L256-259. That would affect Rsed, but not K values, as the surface for microbial attachment of cotton strips would be independent of the sediment. What about other factors? Aridity usually results in higher temporal variability in flows, lower nutrient concentration during baseflow, less fungal inoculum, higher deposition of fine sediments, which cloggs intestices...

The sentences referred to are: “If the relationship between decomposition and D50 is causal, it could be mediated by the total surface area available for microbial attachment. Coarser sediments have much less surface area, potentially limiting overall microbial activity.”

We plan to revise the sentence to something like: “If the relationship between decomposition and D50 is causal, it could be mediated by the total surface area available for microbial attachment. This would, however, influence decomposition only to the extent that microbial biomass in adjacent sediments impacts microbial activity on the cotton strips.”

L273-275. Not convincing. These authors show that a large fraction of respiration comes from the degradation of labile carbon produced by photosynthetic organisms, but this should have no effect on cotton decomposition, unless you are talking about the priming effect?

The sentences referred to are: “Though not measured here, less light could suppress autotrophic production which will limit heterotrophic respiration (Bernhardt et al., 2022; Mulholland et al., 2001; Young and Huryn, 1999) and, in turn, indirectly lead to slower decomposition relative to high light leading to priming organic matter degradation via labile carbon derived from phototrophs.”

We plan to revise the sentence to something like: “Though not measured here, reduced light could suppress autotrophic production, which may limit heterotrophic respiration (Bernhardt et al., 2022; Mulholland et al., 2001; Young and Huryn, 1999). Lower autotrophic production could therefore slow decomposition relative to high-light conditions by reducing the supply of labile carbon from phototrophs that can prime organic matter degradation (Danger et al. 2013; Howard-Parker et al. 2020).”

Thank you for the suggested edits. Below we respond to each comment with our planned revisions. Our text is in bold font, while the reviewer's text is in normal font.

Reviewer 2:

This MS describes the results of a comparison of cotton strip decomposition rates within the riverbed with whole ecosystem and water column respiration rates measured at the same set of sites across the Yakima River Basin. The authors found that cotton strip decomposition rates were more closely related with whole ecosystem respiration than they were with an estimate of sediment-associated respiration calculated as the difference between measured whole ecosystem and water column respiration rates. The MS is generally well-written and will make a useful contribution to the literature on the relative contribution of different elements to overall river ecosystem respiration.

Thank you for the encouraging remarks. We are pleased that Reviewer 2 feels our study will make a nice contribution to the literature.  Below we respond to their suggestions in more detail.

My main concern with the MS relates to the use of the term sediment-associated respiration (ERsed). My initial perception was that this parameter represents respiration within the sediment beneath the riverbed, when in fact it represents respiration both within and on the riverbed. I think this needs to be emphasized early in the MS so readers are clear about what this parameter really represents. Importantly, a large component of ERsed may be attributed to autotrophic respiration from periphyton and aquatic plants growing on the riverbed and not associated with heterotrophic carbon decomposition. Therefore, there is less expectation that there should be a strong link between ERsed and cotton strip decomposition rates within the bed.

We plan to revise the first paragraph of the Introduction to clarify that ERsed can be attributed to respiration of autotrophs, heterotrophs and other components of stream ecosystems.  Note too that we return to this idea about autotrophic respiration in the Discussion, so this comment that relates to the Introduction helps us go full circle in how we present our research. 

It would also be useful for the authors to emphasize what other elements might be included in the ERsed parameter, since it was not measured directly. For example, has the potential impact of low DO groundwater inputs on whole ecosystem respiration been accounted for?  Could chemical oxygen demand contribute to some of the ERsed?

This is similar to a comment from Reviewer 1, and we provide the same response here. That is, we plan to include caveat statements in the Methods and in the Discussion, per the reviewer’s suggestion. We will inform these caveat statements with stream metabolism literature as all stream metabolism research using single station dissolved oxygen sensors have the same caveats. Note that we kept these additional text elements short since the metabolism results are published in prior work.

I’m also concerned about whether the overall weak relationships between point-scale cotton strip decomposition and reach scale measures of respiration primarily reflect differences in the scale of measurement rather than poor linkage between different components of the river ecosystem. I’d like to see some evidence in the MS that 4 replicate measures of cotton strip decomposition are sufficient to represent small-scale variability in decomposition at a reach scale. How did within-reach variability compare with between-reach variability in cotton strip decomposition? At the very least, this issue deserves some attention in the discussion.

These are important points and we appreciate the chance to address them in the manuscript.  The weak relationship between ERsed and our measurements of decomposition likely stems from several factors. Indeed, our habitat-scale measurements of decomposition rates are at a much finer scale than those of whole-stream metabolism, and there are localized environmental factors that probably influenced decomposition rates, but not reach-scale metabolism (e.g., very localized areas of downwelling or upwelling). We do not have evidence that our 4 measurements of decomposition rates in our study are sufficient to capture the small-scale variation in decomposition; to address variation within reaches, however, we deployed our experimental units at locations that we felt were representative of that reach in terms of sediment size, flow velocity and substrate size. Variation in decomposition rates within our reaches was undoubtedly a source of statistical noise that weakened the relationships we observed, and we plan to detail this caveat in the revised manuscript.

I note that cotton strip decay rates were weakly correlated with both ERtot (R2 = 0.29) and ERsed (R2 = 0.22). Does the slightly stronger correlation with ERtot really justify the key conclusion of the MS that ‘decomposition is the result of integrated processes occurring across the sediment-water continuum’? Presumably there is a strong correlation between ERtot and ERsed – is this correlation presented in the MS?

We think that the stronger correlation with ERtot is certainly interesting, especially since it  is counter to our stated hypothesis. We agree that it is important that we acknowledge the relatively small difference in the R2 between the two relationships. For this, we plan to more directly call out the modest difference in R2 and temper our language to be more conservative throughout the manuscript.

Specific comments:

Lines 220-228: I agree with the comment made by Arturo Elosegi that this part of the MS is very speculative. A measure of algal biofilms on the cotton strips may or may not be related to the autotrophic respiration component of ERsed.

The sentence referred to is: “We propose that if our deployment configuration was complemented with a simultaneous deployment that enabled growth of benthic algal biofilms on the cotton strips, the combined decomposition from both deployments would capture substantially more of the processes that contribute to ERsed.”

We plan to revise the sentence to something like: “We propose that if our deployment configuration was complemented with a simultaneous deployment that enabled growth of benthic algal biofilms on the cotton strips, the combined decomposition from both deployments could--in some systems--capture more of the processes that contribute to ERsed.”

Line 402: remove ‘++’ from within the title of this reference

We plan to make this change.

Line 570: ...shown WITH solid black lines….

We plan to make this change.

Thank you for the suggested edits. Below we respond to each comment with our planned revisions. Our text is in bold font, while the reviewer's text is in normal font.

Reviewer 3:

Stegen et al investigate the relationships between organic matter decomposition and reach-scale respiration. The authors address a relevant topic in freshwater science and the manuscript is well-written. However, I find the study not scientifically sound given strong methodological limitations and data interpretation. The authors hypothesised that organic matter decomposition rates in sediments, calculated from deploying cotton strips in the shallow hyporheic zone, positively correlate with reach-scale sediment respiration (ERsed). Not surprisingly, the authors found a weak correlation between both variables. This is likely due to the deployment method of the the cotton strips (cages), which results in experimental conditions that do not mimic the complexity of the shallow hyporheic zone. Although the authors recognised this limitation in lines 220-225, they wrote the manuscript as if they actually measured organic matter decomposition rates in sediments, which they did not. I recognise the sampling effort but I believe the authors need to reframe the manuscript.

As noted, the relationship between our measured values of organic-matter decomposition and stream respiration were not strong (R2 values in the 0.20s) – this is often the case with ecological field studies. Despite not being strong, they were significant and showed a pattern opposite to our hypothesis, which we found very interesting. We also found other notable results including an extremely broad range of decay rates within a small geographic area, impacts stemming from human activities, and a novel and useful approach for assessing microbe-driven decomposition rates in the hyporheic (cotton strips in widely available metal cages).  We agree that our experimental conditions do not fully mimic the complexity of the shallow hyporheic, but our methods do provide a useful proxy for microbially-driven decomposition of particulate organic matter. 

We also agree with the comment “they wrote the manuscript as if they actually measured organic matter decomposition rates in sediments, which they did not.” It is important to contextualize this. Most decomposition studies (and there have been thousands) measure organic-matter decomposition potential, that is, the capacity of the ecosystem to decompose organic matter (e.g., using litter bags). These studies, like ours, do not take into account full system complexity or how much organic matter is actually being decomposed in the ecosystem. This is a widespread semantic problem in the literature and Reviewer 3’s point is valid. To address this we plan to include language throughout the manuscript (abstract through discussion) to clarify that our approach (like thousands of studies before us) quantifies organic-matter decomposition potential. Thank you for encouraging us to be more precise.

Major comments

lines 193-208. The relationships between Kcd or Kdd and drainage area are rather weak, yet significant. Did the author consider using land use/land cover instead?

Please see Table S1, which reports results from the LASSO analysis. That analysis included land cover variables, which were not selected in the LASSO modeling as being explanatory.

lines 133-135. Please indicate the number of observations where the tensile strength was assumed as 0.05. The authors should provide an strong case for using this approach. There are robust statistical methods to deal with non-detects (in this case, values equal or lower than the lowest tensile strength).

We will include the number of ‘non-detects’ in the manuscript, which was 5.4% of cotton strips. We know that there was more degradation that occurred in these non-detect strips than would have been measured at the limit of detection. We need to include such information in the analyses. To entirely remove these samples would bias the analyses away from conditions with very fast rates of decomposition. We cannot use a tensile strength value of zero because that would cause the decomposition rate to be undefined, due to taking the log of the tensile strength ratio (see Eq. 1). Using half of the detection limit is a practical compromise. 

To address the reviewer’s concern, we plan to include additional caveats in the Results and Discussion to highlight that having non-detect cotton strips adds some uncertainty to the study’s outcomes, and that this uncertainty should be relatively small given the small fraction of non-detect cotton strips. We will also add more rationale to the Methods section explaining why we used half of the LOD (and not zero) and note that using this approach provided data that aligned with rates observed across global scale efforts.

lines 262-265. These two studies are not comparable due to methodological differences.

We agree that there are methodological differences, and as noted in the manuscript, we believe that these explain the discrepancy in research outcomes. The cited study allowed access to the organic matter by macroinvertebrates and ours did not. The manuscript directly acknowledges this and uses it to help explain differences in outcomes across the two studies. We prefer to retain this text.

Minor comments

line 19. The sentence is unclear

We plan to clarify the sentence.

line 122. Revise the sentence "... and clean 70% ethanol was..."

We plan to revise the sentence, likely splitting it into two sentences.