the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
| 02 Sep 2024
Continuum modeling of bioclogging of soil aquifer treatment systems segregating active and inactive biomass
Abstract. Soil aquifer treatment (SAT) systems are used to remove pollutants from treated wastewater and store freshwater for reclamation and reuse. However, the accumulation of microbial biomass in the soil pore space, bioclogging, reduces water infiltration and hinders SAT efficiency. Since SAT systems play a crucial role in maintaining water resilience by providing an alternative to freshwater supply, optimizing their operation is essential to ensure their effectiveness. However, SAT systems are complex and dynamic systems that involve coupled interactions between microbial activity, water infiltration, and bioclogging in unsaturated media. This work proposes a continuum model that accounts for all these processes while distinguishing between active and inactive biomass, with the latter split into labile and recalcitrant fractions. The model is used to replicate a laboratory column experiment of bioclogging under unsaturated conditions and to explore how to optimize the operation of SAT systems. Specifically, we determined optimal wetting and drying periods that maximize water input to the SAT system while maintaining nutrient transformation rates. Our simulations show that the dry/wet time ratio controls biomass spatial distribution over depth. In contrast, the dry time extent dictates the degree of recovery of the soil relative to its initial (clean) infiltration capacity. We discuss the potential of this model to be extended to larger-scale experiments and to inform daily SAT operations in the field.
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RC1: 'Comment on hess-2024-251', Guillem Sole-Mari, 12 Oct 2024
I think that the paper is of good general quality, with clear and well-structured writing, and a valuable scientific contribution overall. After having read (and quite enjoyed) the manuscript, I only have a few comments, many related to clarity and rigor of equations and symbols. However, I would also like the authors to discuss with care the representativity of their results based on the choices made regarding configuration parameters (see comment on Line 191). All comments below:
Equation 1 and elsewhere: I think it is formally wrong to define K(h) and K(n) with the same exact symbol, which would seem to imply that they are the same exact function, and that here you just evaluate it for either h or n. You should use two different symbols for these two different factors.
Equation 2b: I think you should point out at some point that the capillary head h is always negative, even if that might seem obvious to the authors, I think it is worth clarifying in order to ensure good interpretation of the equations with the minus signs in front of alpha h.
Equation 5: There seems to be a typo, the advection term should indicate the divergence of qCi (mind the dot as well as the parentheses).
Equations 5 and 6: Each species Ci should have a different reaction rate Ri, which is possibly a function of many other different “Cj”. I believe you are wrongly using the parentheses (which should stand for “function of”) as if they were part of the function’s symbol. Brief: Ri, not R(Ci), and same for equations 6.
Line 100: X X
Equations 9 and 10: Same comment as eq 5 and 6.
Lines 182-185: So you imposed a fixed gradient boundary condition at the inlet which changes over time in order to always get the 1mL/min inflow (or 0mL/min in dry conditions) ? So you kind of imposed a fixed flow at the inlet boundary, or how is it different? Also, this reads “as shown in Figure 3”, but Figure 3 doesn’t really show much about how the boundary conditions are implemented. Maybe Figure 3 could indeed be improved to include more information.
Line 191: Why that choice of 450min? (which to me would seem like quite a short wetting time for operational realism). Later (section 3.5) you do seem to confirm this suspicion by finding quite a longer optimal cycle time, but at that point you have already fixed the dry-wet time ratio at 4.5. This leaves me wondering, for instance, if there isn’t a more optimal strategy that uses rather long drying periods and also a lower dry-wet time ratio maximize hydraulic loading (unless I am missing something). I guess you could say that this is a first attempt and a framework which can be used for further investigation and optimization, but I think that some discussion around this possible limitation of the study is missing. In other words, you do discuss as of now that there are these two configuration parameters (wet-dry time ratio and dry time), but it should be made clear that there is probably a complex interplay between them and that for instance, for each different dry time, one may find different results regarding the role of the dry-wet time ratio.
Line 295: I would say it as “Therefore, our results would suggest that neither…”. Mostly because like I said earlier, you have not really simultaneously explored different ratios for different drying times.
Line 325: ,,
Sincerely,
Guillem Sole-Mari
Citation: https://doi.org/10.5194/hess-2024-251-RC1 -
RC2: 'Comment on hess-2024-251', Anonymous Referee #2, 17 Oct 2024
The manuscript “Continuum modeling of bioclogging of soil aquifer treatment systems segregating active and inactive biomass” by Saavedra Cifuentes et al. presents a numerical modeling study on the potential impact of dry and wet cycle iterations on the performance of soil aquifer treatment systems. The conceptual model approach considers different biomass pools (active cells, EPS, dead cells) each having its specific dynamics and contributing to changes of the hydraulic conductivity due to bioclogging. Data from a column experiment were used as a reference and subsequently the model was used to predict in influence of different configurations of dry and wet cycles on the exhibition of bioclogging and on the overall hydraulic performance of soil aquifer treatment systems.
General comments:
In general the manuscript is well written but exhibits some inconsistencies in the description of the used model approach – see specific comments below.
I acknowledge that the presented conceptual approach dividing the biomass into different pools is meaningful and consistent with other approaches presented in the literature. It is thus a valid hypothesis. However, I am not convinced how this hypothesis is tested/verified with results from the column experiment. There is indeed a match between the spatial distribution patters on measured and simulated biomass but this comparison is done solely for the biomass and for a single observation time only. No comparison between measured and simulated substrate/electron acceptor concentration are shown and no comparison between measured and simulated changes of the flow dynamics have been shown either. Furthermore, I have the impression that the flux boundaries considered in the model are not adequate to describe the experimental conditions (or they are described in an insufficient way – see specific comments below). Therefore, other (less or equally complex) conceptual approaches might also explain the shown observations. The same holds for the parameters used in this study. Most are taken from the literature but literature values for parameters describing microbial dynamics can easily vary by at least one order of magnitude and so does then vary the dynamics of the biomass itself. The presented results on the influence of the dry/wet cycle configuration might thus be biased. All this leads to the present study discussing the potential effects on clogging in SAT systems based on a reasonable but unverified hypothesis, only.
I am not an expert for SAT systems but from their description I would assume that clogging at the bottom of the infiltration ponds is not only caused by microbial growth but also by the deposition of particles and organic material. How does this interfere with the discussed variations of the dry and wet cycle operation? Out of curiosity, I am also wondering if it is practically possible to tune the length of the wet cycle for a system affected by clogging – at the end a given amount of water is entering the pond and then infiltration takes as long as it takes. Similarly I am wondering if evaporation from the soil system during the dry cycles (especially in semi-arid regions) is interfering with the clogging effects, but I am aware that this is not the subject of this study.
Specific comments:
To my opinion the term “inactive biomass” is misleading since is it typically associated with biomass fractions (e.g., dormant cells or spores), which can turn into active biomass. In the present study the “inactive biomass” consists of EPS and dead cells. Some re-labeling of these pools might be helpful to avoid misunderstandings.
Eq. 6b, l 104: Is this equation correct? If I insert the definition of ζ_O2 into Eq. 6b the term into the brackets and thus phase transfer rate approaches the non-zero negative value of -s_w*C_02 at saturation.
Eq. 7: I agree that pore-availaibility can limit microbial growth, but here is it assumed that microbial degradation activity is decreasing when the biomass is approaching the maximum volume. I.e., at highest biomass concentrations the activity is minimized. Some discussion on this would be needed.
Fig. 2, Sections 2.2 and 2.3: In the Introduction and in Fig. 2 the model is introduced as considering different microbial processes incl. nitrification and denitrification but in Sections 2.2 and 2.3 only aerobic heterotrophs and their activity are described as part of the model. Clarify/correct.
Section 2.5: Was there any DOC present in the injected water or how was the carbon source applied? Are there any measured data on this which could be used for model verification? How long did the experiment last? Was there any measurement of the water fluxes at the effluent?
L 177 adjust brackets around reference.
L 178/179: Ok for the column experiment, but see also comments above on composition of the clogging layer. I guess the SAT optimization model is not describing a column experiment. Anyway, this discussion does not belong to this section.
L 182: Figure 3 does not provide such information.
L 182-184: I do not get this. If the gradient is adjusted to maintain a given flux how does clogging result in a decrease of the simulated flux? To me it seems that constant flux conditions are simulated (at least during the wet periods) but later on the manuscript shows changes in the influx due to clogging are presented?!
Tab. 2: Correct unit for “Half-reaction constant for electron acceptor”
Tab. 2: Why is a parameter for a nitrogen source given here? This is not mentioned in the equations given Sections 2.2 and 2.3.
Tab. 2: The term “biodegradable fraction of dead biomass is misleading/incorrect”. Both fractions of inactive biomass are decaying via hydrolysis.
Tab. 2: Adding up the true yield and the fraction used for EPS gives a total fraction of 0.67 of DOC being converted into biomass. This sounds rather high. Comment/discuss.
Units: The units used in Tabs. 1 and 2 are different than the units used in the text. While I understand the reasons for this, this is inconvenient for comparing text and table values.
L 187-189: Provide some further information on the biomass density. Is this given as dry mass per wet volume or carbon mass per volume or something else. Since the yields are dimensionless I guess it is DOC mass per volume of biomass. Assuming the latter the presented value is in agreement with literature values for bulk biomass (i.e. bacterial cells plus EPS etc.) and the rather low value is explained by low density EPS forming much of the bulk biomass. To use this value for the active bacterial cells is no well justified since the carbon content of cells is much higher and thus their density also much higher. This implies that with the used density the volume and thus the clogging effect of the active and recalcitrant biomass (living and dead bacterial cells) is overestimated.
Fig. 4: Compare for which cell mass the two curves would match. From Fig. 2 I get the impression that approx. 10^-11 g/cell are considered. Are these values reasonable?
L 200-202: The statement is reasonable but again, are there any measured concentrations from the experiment?
Fig. 5a and c: If you want to emphasize that the flux is going down invert the y-axis (or show the absolute value of the flux). Other wise you rather leave the impression of an increasing flux. Btw., are the no data on measured water fluxes from the experiment?
Fig. 5: Clarify which y-axis values have to be multiplied by which factor. The “1e-6” seems to be out of place and the “x10^-2” might belong to panels a/c or b/d.
L 227/Figure 5c: I do not see specific dips in the influx which I could attribute to the dry periods. It appears as if the influxes gradually decrease which is not what I would expect for a dry period.
L 232: There is no consumption of inactive biomass by the active cells described by the equations in Sections 2.2 and 2.3.
L 235-236: Unclear/rephrase. Is the mentioned hydraulic loading the average loading rate at quasi-steady state or including the initial phases, too? From Fig. 5 I get the impression that 2.3x10^-2 m/s is rather the initial value and not the long term value.
L 254-256: Clarify. From this sentence I is not clear to me what you define as long-term hydraulic loading rate. Clarify also if the presented values are averages for a full wet/dry cycle (or if they are something else).
L 264 and below: Here it would be highly interesting if the shown biomass distributions are at or close to steady state (I guess not) or if they would approach a different distribution at later times. Since the clogging effects are mainly caused by the high biomass concentration at the vicinity of the inflow a steady state of the fluxes does not necessarily imply a steady state of the biomass in the downstream regions. It would also be good to show some substrate concentration results as they would indicate if growth would be possible in the deeper regions of the columns. For the interpretation of the results and for the potential implications for real SAT systems one would also need to know what is limiting microbial activity: depletion of DOC or of O2?
L 282-284: I do not get this statement.
Section 3.5: Similarly to my comment above, I would be good to know if the presented biomass concentrations are at steady state or at least close to it.
L 331-332: Do you have any additional results confirming this statement or is this based on the biomass distribution data only? If the later is the case, I think this statement is misleading.
L 340-341: This is the first time some information on substrate supply in the column experiment is provided. This information and further details should be added to Section 2. Which DOC concentrations was provided in the column experiment?
Citation: https://doi.org/10.5194/hess-2024-251-RC2
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