A well written and valuable contribution. The descriptions of a novel approach to experimentally combine CT-scanning, Os-staining and respiration measurements are useful. And most importantly, I appreciate the creative approach to compute transition probabilities of organic-pore phases and test these as predictor variable for microbial activity. I appreciate the authors’ responses to most referee comments and expect them to implement the presented changes. Still a few issues need to be resolved prior publication:

My major concern is the one as R2Comm4: The volume% of organic matter in the studied aggregates was unusually large. But much seems to be related to the spatial resolution of 3µm. To most readers it would appear that the organic matter fraction was strongly overestimated by the adopted Os-staining procedure and that OM densities of 0.4g cm-3 are extremely low. Usually adopted values are 1.4 (e.g. Chenu et al., 2006 EJSS). Is this discrepancy explained by the simple fact that you are considering ‘bulk’ densities of OM? This would imply that much of the aggregate volume classified as OM in fact includes air inside sub-resolution pores as well. So the question remains how much of the aggregate volume was approximately overestimated to be either mineral or organic because pores<3µm were misclassified as being OM or mineral matter? This needs to be addressed still in the manuscript and it should be stipulated that the OM densities in table 1 represent apparent bulk densities.

I concur with the authors that no new proof needs to be presented for the validity of the Os-staining procedure (R2Com2 & 3). Nevertheless the authors should acknowledge that Os-staining of OM sorbed onto mineral particles could have resulted in misclassification of voxels that are partly OM and partly mineral matter as being entirely organic. There is no way of confirming this because such edge effects are only visible at finer spatial resolutions. This knowledge should, however, be taken along when critically assessing the quantified volumes of organic phase and OM densities. Most likely the OP and MP values are also strongly underestimated as compared to the physical reality in which many sub-resolution pores are in contact with both organic and mineral phases, especially so in clay soil. So again the computed probabilities are estimates based on CT-images, which also only apply to the spatial resolution at hand: The probability of OM to be in contact with a pore >6.6µm is 0.02-0.03. The actual OP at finer resolution is likely much larger. This needs to be properly explained in the discussion and certainly in Figure 7’s caption.

The value of calculating semi-variogram ranges for all three soil phases is less apparent. I found Fig. 9 overloaded and table 3 redundant. There is really no need to present semi-variogram ranges for the mineral and pore phases so please remove these from Fig. 9 and omit Table 3. You could indicate the median range values (in µm) within Fig. 9.

The statement ‘The transition probabilities between OM-centred voxels and adjacent pore voxels – a measure of OM accessibility – were both small and of limited variation (probabilities between 0.02 and 0.03) for all aggregates and there was no clear relationship between accessibility and the magnitude of SHR.’ In the conclusions stands a bit isolated. So what is your conclusion now: is it still worthwhile calculating transition probabilities? What about calculating these for transitions in future from OM to specific pore size classes,…

The statement ‘shorter length scales of OM variation leads to greater frequencies of microsites and greater CO2 production through microbial respiration and we present preliminary evidence to support this relationship.’ in the conclusion is interesting. In practice a larger range could represent the presence of more larger particulate OM particles, with many OO transitions over considerable distance (even milimeters). If aggregates contain much particulate OM the OM variation scale / respiration relation could also be inverse: fresh organic substrate particles encapsulated in aggregates (e.g. plant litter) may be more labile, resulting in a higher soil respiration than in a soil aggregate with an equal amount of OM, which is instead mineral-bound. I would be happy if the authors could comment on this in their discussion.


R1Com1. I agree to referee 1’s main comment. The provided pore shape factor F on its own does not well quantify phenomena like tortuosity. I also follow the authors in that data presented in Figs. 4 and 5 should not be omitted.

R1Com4 please add a sentence explaining the purpose of beading the aggregate in glass beads

R1Com5 I appreciate the authors’ initiative to as far as possible enable reproduction of their work by detailing the workflow of the CT volume processing. However, section 2.5.1 was pertinent because of the specific packing of aggregates in quartz beads. The relevance of this section may be small in future experiments with other ways of packing soil samples. So I would ask the authors to move the stepwise listing presented in 2.5.1 to supplementary material.

R1Com6 Indeed some aggregation is mostly unavoidable as of yet, this seems acceptable.

R1Com 11 I follow referee 1 but ok with the authors’ response. However Fig6’s caption is confusing because presently only pertaining to the OM transitions. Needs to be updated

R2Com15 ok with authors’ response, but could this point not be added to a perspective for a future relevant avenue?

Minor comment:
Fig 4 please use more standard Y-axis tick marks (104, 105,…)
Fig. 6 something is wrong with Fig6’s Y-axis
P14L1 ‘is from:to the organic phase’ is something missing here?

The authors admit that their previous approach to calculate soil phase densities and volumes was wrong. They have now adopted an alternative pragmatic approach. True progress indeed only results from acknowledging former mistakes and I very much appreciate the authors’ willingness to do so. The analysis has been greatly modified accordingly. Referee comments have been properly addressed. I only have a few more (minor) remarks.


A concluding phrase to end the abstract remark is missing
P4l25 provide volume of subsample taken for CO2 analysis
In fact the procedure used to quantify soil respiration is crude and a better approach would have been to collect multiple gas samples over time. At present we
P8l5 ‘We then computed the threshold adsorption value at 56 keV that equated to the transition from pore (smaller adsorption) to solid phase (larger adsorption)’
I’m sorry but I don’t really understand. Does this mean that you empirically determined the threshold grey value based on local minima in the summed histogram of the entire aggregate? Or is the threshold theoretical by comparing X-ray attenuation of air and mineral matter? Or did you per aggregate set the threshold grey value so that the total number of voxels assigned as pores equated to Vp / volume of one voxel?
Needs further explanation.

P8l6 ‘value’ instead of ’values’
P10l13 ‘excess CO2 concentration’ sounds awkward. Would be better to use just omit ‘(based
on the excess CO2 concentration scaled to the TOC content)’ from this sentence. The actual unit of your reported ‘respiration’ is not µg C mg C-1 but in fact µg C mg-1 day-1. Consider revising.
p13 l4-7 Difficult sentence to follow. Please rephrase (perhaps split in two)
Discussion/conclusion: At present only a 24h incubation has been used to estimate microbial utilization of the native SOM present in the aggregates. It is well known that cumulative C-mineralization usually follows a non-linear course. Firstly: SOC is inherently composite and exists of a continuum of decomposability and so after depletion of C respired at a high rate from labile constituents within a few days, only slower respiration indicated by a more gradual CO2 emission following a 0-order kinetic is usually observed. In the present study we are merely looking at a quantification of the breakdown of the most labile parts. Their content may well have differed among the studied aggregates. Likely this is then what dominantly determined the variation in total respiration over 24h. It is then also evident that only weak correlations with quantifications of pore structure or physical distribution of the OM were found. Secondly, it is well known that drying leads to death of microorganisms and a peak C-mineralization flush after rewetting is related to the microbial processing of this necromass. Again the time frame of the soil incubations was likely too short to have a representative measure of microbial utilization of the majority of OM present. Alternative mechanisms explaining transient effects of soil moisture changes on microbial activity have been grouped under the term ‘Birch effect’. I would ask the authors to be more critical in their discussion and conclusion on the relatively limited approach used to assess microbial processing of native SOM.

Dear Dr Rawlins,

After carefully reading the review reports and the revised manuscript, I am happy to accept the paper for publication. Thank you for considering SOIL as an outlet for this interesting and novel study.

Kind regards,

Kristof Van Oost