Author response:
The following is the authors’ response to the original reviews.
We thank the Reviewing Editor, the Senior Editor, and the three reviewers for their careful and constructive assessment of our manuscript. We were encouraged that the reviewers found the question timely and novel, the experimental design thoughtful and well-replicated, and the analyses diverse and informative. The reviewers also raised a number of valuable concerns, which clustered around three themes: (i) the framing of host-mediated selection as microbiome “engineering” versus a proof of concept; (ii) the interpretive challenges introduced by microbial dispersal and the resulting limits on the sterile-inoculated controls; and (iii) requests for clearer methodological detail and additional context from the recent literature. We have revised the manuscript to address these points through clearer framing, expanded discussion, and fuller methodological detail. Consistent with the nature of this long-term experiment, our revisions strengthen the interpretation and presentation of the existing dataset rather than adding new experiments.
eLife Assessment
The study has also shortcomings in that the rescuing effect is not benchmarked against healthy well-watered plants, the sterilized controls do not add much information, and the dispersal between inocula confounds the interpretation of the results… the presentation would overall benefit from more extensive consideration of recent developments in the field.
We appreciate this balanced summary and have revised the manuscript accordingly. We have reframed the abstract and Introduction to present the study explicitly as a proof of concept rather than a completed engineering effort (ll. 27–31; ll. 96–101); we now address the well-watered benchmarking limitation and the limits of the sterile-inoculated controls directly in the Discussion (ll. 543–551); we discuss dispersal and its confounding effect on interpretation head-on, including an alternative hypothesis (ll. 546–551); and we have incorporated the recent studies suggested by Reviewer 3 (ll. 206–209, 442, 476–478). Each change is detailed in the point-by-point responses below.
Reviewer #1 (Public Review):
Weaknesses:
The findings demonstrate the efficacy of host-mediated microbiome selection, but the engineering part for enhancing rice performance under drought-stress conditions has not been provided. The proposed mechanisms rely on correlations but not direct experimental proofs.
We agree, and we have adopted this framing throughout. Our study demonstrates host-mediated selection as a discovery framework rather than a completed engineering pipeline, and we now say so explicitly: the abstract has been reframed (ll. 27–31) and a statement added at the end of the Introduction (ll. 96–101) clarifying that the work reproducibly enriches beneficial taxa and functions and yields simplified candidate communities, but does not yet benchmark those communities against single-isolate inoculants or test them in the field or against a resident native microbiome. We likewise agree that the functional inferences from our metagenome-assembled genomes (MAGs) are correlative; we now state this explicitly in the Methods and Discussion (ll. 776–778) and note that establishing causal roles for individual taxa or genes will require targeted isolation and genetic manipulation.
Reviewer #1 (Recommendations For The Authors):
The experimental design… could benefit from more detailed explanations. For instance, what are the criteria for choosing these soils and how are they relevant to rice growth phenotype? Also, the word ‘generation’ is misleading as it implies the use of seed-to-seed experiments… It would also be good to explain why the authors chose 6 generations for rice fields and 4 generations for deserts and serpentine seep. Importantly, the contribution of the rice seed microbiome… has not been considered and is also missing from… the discussion.
We have addressed each part of this comment. Soil selection criteria: the Results section “Source inocula bacterial diversity” describes our rationale — we screened nine field soils in a pilot experiment, then selected the three that both supported rice growth and had negligible taxonomic overlap (providing three distinct starting points), with a stated per-soil expectation (rice-adapted, drought-adapted, and high-diversity). We are happy to expand this further if the reviewer feels additional detail is needed. “Generation”: we now define this term as a single 40-day selection cycle rather than a seed-to-seed generation (l. 109). Six vs. four generations: we explain in the Results (l. 309) that, having observed convergence of microbiome composition across soil treatments by the fourth selection generation, we concentrated resources on Rice Field and carried it through two additional cycles. Seed microbiome: we have added a note to the Discussion (ll. 444–446) that, although seeds were surface-sterilized before each generation, a residual contribution of seed-borne endophytes common to all treatments cannot be excluded.
The authors stated that microbiomes were not selected for propagation into future generations in control lines. In this case, have the authors tested if the control LI microbiome in SG1 through SG6 did or did not significantly change in all the soil types?
We have clarified the role of the live-inoculated (LI) lines in the text. LI lines were well-watered controls that were re-inoculated each generation with unsterilized selection-line material; they were included to identify drought-enriched taxa (by contrast with the droughted selection lines) and to test whether drought-optimized microbiomes were deleterious under well-watered conditions — not as an independently propagated selection line. Because LI communities were re-derived from selection-line inocula each generation, their composition necessarily tracked the changes occurring in the selection lines; this is the basis of the SL-versus-LI differential-abundance analysis (Figure 7B, Supplemental Figure 9). We note that comprehensive, temporally resolved 16S sequencing was performed for Rice Field, so we are appropriately cautious about extending LI comparisons across every soil type, and we have tempered our conclusions from the control lines accordingly (ll. 543–551).
In Figure 3B (rice field), the tolerance in terms of AUC NDVI contrastingly increases to the biomass values in SG5 and SG6… the [NDVI] does not seem to be a good measure… It would be interesting to analyze these data sets under normal conditions… include representative pictures of all the ‘generations’… It will also be important to include the LI control data in Figures 3B and 3C.
We appreciate these suggestions and respond to each. Our metric is biomass-adjusted AUC NDVI, which we use precisely to separate drought performance from plant size; NDVI itself was validated against shoot water content in preliminary experiments (R = 0.98; Supplemental Figure 2E), so we are confident it is an appropriate, validated proxy for drought status. We have substantially expanded the Methods to explain this adjustment and why the metric can diverge from raw biomass (ll. 666–669). Regarding the specific additions requested: analyzing the well-watered plants as a phenotypic dataset, adding representative images for every generation, and plotting LI data in Figure 3B/C would each require new analyses or figures that are outside the scope of this revision; moreover, LI plants were never droughted and therefore have no drought-response score comparable to the SL and SI lines, so they cannot be placed on the same axes. Representative images contrasting the first and last selection generations are already provided in Figure 3A. We have, however, added an explicit acknowledgement that our design does not quantify the absolute magnitude of drought rescue relative to well-watered performance (ll. 551–552).
It is less clear how sterile soils acquired environmental taxa over time. Was this a seepage of microbes from inoculated samples to the calcinated clay, possibly via the water irrigation system? In this regard, four Venn diagrams representing all the generations… would be relevant.
Each plant was grown in an individual container with its own separate water reservoir (Supplemental Figure 4), so shared irrigation was not a route of transfer; the most likely routes are airborne movement and handling within the growth chamber, together with within-treatment shuffling of plants. Our dispersal analysis (Figure 5) already traces the origins of taxa in each treatment, and Supplemental Figure 6 quantifies the ASVs shared among treatments over generations; we have added explicit criteria for these origin assignments (ll. 248–253). We therefore prefer to retain the existing Figure 5 / Supplemental Figure 6 presentation rather than add four separate Venn diagrams, which would convey the same information less quantitatively, but we are glad to reconsider if the editor feels a Venn representation would help readers.
What is the logic behind the so-called ‘immigrating taxa’ in this study?
“Immigrating” (dispersed) taxa are those that appear in a treatment despite not being attributable to that treatment’s own starting material — i.e., ASVs not detected in that treatment’s field soil or enrichment-generation inoculum, which must therefore have arrived by dispersal from other treatments or from the growth-chamber environment. We have made this definition explicit in the text (ll. 248–253).
The decrease in alpha-diversity in subsequent generations… should be thoroughly discussed. Have authors tried to culture these few remaining taxa? If yes… tested for their individual drought tolerance supported by physiological assays… If no, is the microbiome of SG6 (and associated functions) ideal or sufficient to create drought tolerance in field conditions?
We have expanded the discussion of the diversity decline. In addition to niche filtering along the soil-to-root gradient and dilution-to-extinction (already discussed), we now note that DNA-based profiling cannot distinguish metabolically active cells from relic DNA or dormant/non-viable cells, so part of the apparent collapse in diversity may reflect enrichment for the taxa that were active in the original inoculum (ll. 206–209). We agree that culturing the remaining taxa and characterizing them with physiological assays (e.g., water potential, water-use efficiency, stomatal conductance) is a valuable next step; these experiments are outside the scope of the present study, which we have now framed explicitly as a proof of concept, and we identify field validation of selected communities as a key open question (ll. 96–101).
The result that Ideonella was identified as the dominant taxa in all selection conditions is highly interesting… This… should have been followed up for isolating the strains and performing direct tests to test their importance for conveying drought stress.
We agree that isolating and directly testing dominant taxa such as Ideonella is the logical next step, and we now emphasize that a central value of host-mediated selection is that it yields simplified communities from which such taxa can be more readily isolated (ll. 27–31). These isolation and functional-validation experiments are beyond the scope of the current study and we have framed them as future directions rather than undertaking them here.
The MAGs shown in Figure 8 have apparently ‘been assigned to ASVs…’. These data are not shown anywhere… the MAG data only give correlations but not direct genetic proofs of the biological functions of the identified genes.
We have expanded the Methods to describe how each MAG was matched to an ASV (by closest taxonomic assignment and by concordance of relative abundance across samples), and we now state explicitly that these assignments are approximate and that the functional inferences drawn from them are correlative rather than definitive (ll. 776–778). We would be glad to add a supplemental table listing the MAG-to-ASV assignments if the reviewer or editor would find it useful; because it reports assignments already in hand, it requires no new analysis.
Reviewer #2 (Public Review):
Strengths:
I think this study examines an important and exciting topic in the area of plant microbiomes. I predict the findings of the experiments will inform a wide audience of researchers attempting similar studies and be helpful in their designs.
We thank the reviewer for recognizing the novelty of this complex experiment as well as the effort we put into designing it. Like the reviewer, we hope that this manuscript can serve a wide audience and help inform subsequent experiments in this new topic area.
Weaknesses:
Although the controls were well designed, the dispersal of the microbiomes erased the utility of the sterile inoculated (SI) controls… the SI lines acquired microbes from the experiment and never appeared to significantly deviate from the SL plants. The dispersal of the microbes… also minimizes any conclusions that can be made about the different starting inocula and how prone to selection they may be.
We agree that microbial dispersal confounded our ability to use the sterile-inoculated (SI) plants to account for batch variation between generations. By maintaining each plant as a spatially discrete unit (individual pots and watering reservoirs), we had originally intended SI plants simply to acquire a similar consortium of environmental microbiota each generation. Truly axenic SI plants would have been better suited to this purpose, but would have severely limited the number of replicates and replicate selection lines we could include. We have now addressed this limitation directly in the Discussion (ll. 543–551): we state that the SI lines cannot be treated as static, microbe-free baselines, that the batch-to-batch variation they were meant to capture is only partially controlled, and that dispersal limits the strength of the conclusions we can draw about differences between starting inocula. This shared trajectory of selection and intended control lines has been observed in other host-mediated selection studies but rarely discussed in detail, and we now foreground it as a lesson for experimental design.
Reviewer #2 (Recommendations For The Authors):
My first concern is the framing of the approach… the authors never show that this approach has better efficacy than single-isolate inoculates… The phase of the research is still proof of concept, understandably, but these caveats should be mentioned/addressed head-on in the Introduction and Discussion.
We agree and have made these caveats explicit rather than implicit. The abstract now frames the work as identifying candidate taxa and communities rather than delivering a finished engineering solution (ll. 27–31); the Introduction now states plainly that this is a proof of concept that does not benchmark the passaged communities against single-isolate inoculants or evaluate them in the field or against a resident native microbiome (ll. 96–101); and the Discussion reiterates these limitations (ll. 543–551).
I disagree with the authors that the selected microbiota better approximate field conditions (line 55) - because… the diversity of the microbiome is drastically reduced… it is likely that exclusion of taxa is just as important as the passaging of bacterial members to see the desired effect.
We take this point and have revised the sentence at (former) line 55 accordingly (now l. 57): we now say that community-level screening more closely approximates field complexity than single-isolate screens only at the outset, and we no longer imply that the selected (diversity-reduced) communities better approximate the field. We agree that taxon exclusion may be as important as enrichment; this is consistent with our balance analyses, in which the denominator groups comprise taxa negatively associated with phenotype (Figure 7), and with the diminishing returns we observe as diversity collapses. We have also added an explicit sentence to the Discussion (l. 488) stating that the exclusion of detrimental taxa may be as important as the enrichment of beneficial ones, and that a microbiome’s finite membership may contribute to the diminishing returns of selection we observe over generations.
(1) It is unclear what the reason (or methodology) for correcting NDVI by biomass. Much of the findings hinge on corrected NDVI values, so a more thorough explanation of the correction method… would benefit the reader.
We have substantially expanded this explanation in the Methods (ll. 666–669). We now state that biomass and AUC NDVI were anti-correlated (Supplemental Figure 12) and that we adjusted for plant size by taking the residuals of a linear regression of AUC NDVI on shoot dry-weight biomass, using these biomass-adjusted values as our measure of drought performance so that selection would reflect drought tolerance rather than plant size alone.
(2) Are data for panels B and C of Figure 3 scaled?… how can one have a negative area under the curve if all the NDVI values are positive? For panel B, the representative plant images are much larger than 0.8 grams.
This is a helpful catch, and the confusion stems from our terse original description. The values plotted are the biomass-adjusted AUC NDVI (regression residuals), which are centered on zero by construction; negative values therefore indicate poorer-than-expected drought performance for a plant of a given size and do not reflect negative raw NDVI or a negative raw area under the curve. We now explain this explicitly (ll. 666–669). In panel C, shoot biomass is plotted as dry weight in grams; the representative plant images in panel A are qualitative illustrations and are not scaled to the biomass axis. We will make the axis labels and legend state the units and the residual nature of the adjusted metric explicitly (noted in our accompanying figure-revision guide).
(3) The dispersal analysis… What are the criteria for classifying ASVs as specific to an input source? Was it that they were observed in all samples of field soil, i.e. was a prevalence threshold implemented? Could they be observed in any other soil at a smaller threshold?
We have added the criteria explicitly (ll. 248–253). An ASV was attributed to a given soil treatment if it was detected (present/absent) in that treatment’s field-soil or enrichment-generation inoculum samples; ASVs detected in none of the field soils or source inocula were designated environmental in origin (“unk/env”), and ASVs meeting the criterion for more than one treatment were assigned to each. Assignments were thus based on detection in the source samples rather than on an abundance-prevalence threshold within later generations.
This reviewer finds the results around [inoculum source] inconclusive… the serpentine seep microbiome appears to provide more benefit from the first round of selection than any other soil… The slope of improvement… is different between soils, but mainly because the serpentine microbiomes start out conveying greater benefits than the other soils.
We agree the Serpentine Seep result is not clear-cut. The Discussion already presents inoculum provenance as one of several factors shaping the outcome rather than a decisive one, and we have now added an explicit acknowledgement that Serpentine Seep conferred comparatively large benefits in the earliest cycles before plateauing, so its weaker response to continued selection may reflect an early approach to a performance ceiling rather than an inherently poorer substrate for selection (l. 423). We have tempered our “source matters” language accordingly.
Have the authors assessed the biomass and ndvi of the well-watered plants?… showing this data would allow the reader to assess the degree to which the microbiomes are rescuing the plant… and… whether tradeoffs exist… under fully watered conditions.
We have added an explicit statement that our design does not pair each droughted line with a well-watered readout of the same phenotype, so we refrain from estimating the absolute magnitude of drought rescue (ll. 551–552). We note, however, that shoot biomass increased in parallel with drought performance across selection generations (Figure 3C), which provides no evidence that selection for drought tolerance came at a cost to growth under our conditions. Collecting matched well-watered phenotypes to quantify effect size and trade-offs is a worthwhile aim for future work but would constitute a new analysis beyond this revision.
How can the authors exclude the possibility that environmental microbes pre-existing in the growth chamber taxonomically overlap with the field soil-specific microbes?… the alternative hypothesis should be mentioned… A clearer representation of the ASVs categorized as source soil-specific in Figure 5… would be useful and how many of these ASVs make up the bar plots.
We now state this alternative hypothesis explicitly: because dispersed taxa came to dominate all treatments, we cannot fully exclude that taxa shared across treatments were recruited from a common growth-chamber pool rather than dispersing directly between soils (ll. 546–549). We note that the two processes are difficult to distinguish retrospectively, but that the bias of each SI line toward its own treatment’s native diversity (Figure 5) is more consistent with genuine cross-treatment dispersal. Regarding the figure, the number of ASVs underlying each origin category is available in Supplemental Figure 6; we describe in the accompanying figure-revision guide how the Figure 5 legend can be clarified to state the assignment criteria and the ASV counts.
The sterile inoculated plants were a nice control in theory, but I question their utility… A contrast that should be made is the microbiomes of only SI plants. It is striking that sterilized controls assemble and retain more microbes from the unsterilized starting inoculum. I would expect everything to be acquired from dispersal.
We agree, and we have foregrounded this in the Discussion (ll. 543–551). As the reviewer notes, SI communities were biased toward their own treatment’s native diversity rather than being assembled entirely from dispersal (Figure 5) — an informative observation, but one that also demonstrates why the SI lines cannot serve as the clean, microbe-free baseline we had intended. We now treat this as a key design lesson and note that a fully isolated (e.g., gnotobiotic) control would be required to separate these effects in future experiments (l. 560).
Reviewer #3 (Public Review):
Weaknesses:
Sterile/non-inoculated calcined clay also tends to enrich similar microbes… In a future experiment, the work would benefit from including a truly sterile control… the reader may get to wonder whether these efforts are necessary at all… This is discussed across the paper but not directly addressed and I think the manuscript would benefit from a clear argument for or against this idea.
We thank the reviewer for this insightful point and have made our argument explicit rather than leaving it implicit. First, we agree a fully isolated, truly sterile control would strengthen future iterations of this design; the manuscript notes that gnotobiotic plants would be the ideal (if costly) means of achieving this (l. 560). Second, on whether selection is necessary if plants recruit beneficial microbes from the environment: the phenotypic gains seen even in the sterile-inoculated lines do not indicate that selection was superfluous, but rather that those plants recruited from a metacommunity that was itself being optimized by selection in the neighboring selection lines each generation. In other words, environmental acquisition propagated the benefits of selection across the shared growth-chamber environment rather than replacing it. We have clarified this reasoning in the Discussion (ll. 543–551).
Reviewer #3 (Recommendations For The Authors):
It is mentioned multiple times… that host genotype is the driver of the microbiota selection… However, this is not the case [multiple lines] and therefore I don’t find that surprising that there is a convergence of the microbiota across soils and selection rounds.
We agree and have added text making this explicit: all plants were a single, near-isogenic rice genotype, and because host genotype is itself a strong filter on microbiome composition, the use of one genotype — together with shared environmental conditions and selection criteria — makes convergence across lines an expected rather than a surprising outcome (ll. 438–441). We have softened language that could be read as attributing selection to host-genotype variation.
Another possibility… is that those microbes that are found in the later generations are actually the ones that were active/alive in the initial inoculum. It is not possible to rule out that most of the sequenced microbes in the input were not actually dead. Similar observations were made… in Duran et al. 2022. New Phytol.
We have added this possibility to the manuscript, noting that DNA-based profiling cannot distinguish metabolically active cells from relic DNA or dormant/non-viable cells, so part of the apparent diversity decline may reflect enrichment for the subset of taxa that were active in the original inoculum, with reference to the transplantation work the reviewer cites (Durán et al. 2022; ll. 206–209).
In the shotgun data, was there any observation of other microbes present (fungi, virus)? Did they follow the same trends as the bacterial communities?… I think addressing this will be very interesting and very novel.
We agree this is an interesting question. Our shotgun workflow was designed and assembled specifically to recover high-quality bacterial and archaeal MAGs, and a rigorous cross-kingdom analysis (fungi, viruses) would require dedicated, eukaryote- and virus-specific assembly, binning, and reference databases — a substantial new analysis that lies outside the scope of this revision. We therefore flag cross-kingdom community dynamics as a promising direction for future work rather than presenting a new analysis here.
Any interesting overlap with the results found in Karasov et al. 2022 (biorxiv)?
We have added a comparison to drought-driven selection on host-associated microbiomes in Arabidopsis (Karasov et al. 2022) at the relevant point in the Discussion (l. 442).
In Liu et al., 2024 Nat. Comms, the authors found Devosia as an interesting candidate for disease suppression (to add to the discussion?).
Added — we now note that Devosia, one of the lesser-known genera enriched in our experiment, has recently been highlighted as a candidate mediator of disease suppression in the rhizosphere (Liu et al. 2024; l. 476).
Lipids as a signal for host-microbe interaction: Rich et al., 2021 Science.
Added — in the functional-enrichment discussion we now cite lipids as increasingly recognized central signaling molecules in host–microbe symbioses (Rich et al. 2021; l. 478).
