Interactions with a Complex Microbiota Mediate a Trade-Off between the Host Development Rate and Heat Stress Resistance

Round 1

Reviewer 1 Report

Dear authors,

 

I enjoyed reading this paper, with experiments that take C. elegans out of it’s laboratory cage and test what it means to grow these animals in a more realistic setting resembling a possible habitat with a more diverse array of food. The paper shows interesting results on the impact of different microbiota on development and heat-stress resistance. I think this papers has its merit, but I think it requires discussing and exploring alternative explanations on their observations.

 

Major concerns:

My fist concern is that this study uses the N2 strain in an experiment that places it in a more natural, anaerobic environment. There has been selection on an aberrant oxygen response, that makes that this strain has some drawbacks in using it in these conditions (reviewed in PMID: 25804345). I think this should be a discussion point and taken in consideration when interpreting these results. In my opinion, it is unclear whether the same response is to be expected for other strains.

 

My second concern regards the confounding effect of nutritional status in the microcosm experiments. Is there a possibility of less food being available for the nematodes by ‘growing’ E. coli OP50 in compost? Is there plenty bacterial biomass? The results presented in figure 3 made me ponder whether the trade-off is simply due to nutritional status and developmental effects. This point should be thoroughly examined (PMID: 24780523) and assessing the same developmental stage is very important.

 

Minor concerns and remarks:

Line 35-36: I fail to see how the genetical homogeneity of isogenic C. elegans reduces variation in microbiome composition. I see that there is a core gut microbiota, but does it also not depend on the environment? It would be good to lay a bit more ground work to cover this.

 

Line 61: what is the difference between OP50 and OP50-1?

 

Line 76: do you have a picture of a microcosm? It would greatly aid me in understanding what this looks like.

 

Line 91: how were the nematodes stage-matched? Does that mean that for each repetition the same stage was used?

 

Line 137: ...development, we wished...

 

Line 138: ‘to affect’ should be ‘affected’

 

Line 139: while I fully agree that these microcosms are a lot more natural than the NGM plates we normally tend to use, I do think these should be described as ‘a’ habitat. There could even be different types of habitats with different selection pressures associated with them (e.g. PMID: 31548647).

 

Figure 1: Why are representative experiments shown in B and C? Is there a lot of variance between batches where the relative effects are still similar? I would like the other experiments to be shown in the supplementary. What is represented by a, b, c, d in figure 1A? What is represented by a, b and c in figure 1B? Also, in figure 1A and 1B the lines for Live CEent1 and Live EC are exactly the same, are they there as reference? Than this should be indicated.

 

Line 163-165: No, not in the setup, but it’s hard to draw firm conclusions from ~30 animals per group. What could you see (PMID: 28713422)?

 

Line 165: what does ‘They’ refer to?

 

Line 167: remove ‘a subsequent’, I assume it is ‘...following heat stress.’?

 

Line 168-170: that is in line with literature (e.g. PMID: 24780523)

 

Figure 2: In B and C, what does each dot represent, a worm? How many worms were counted per experiment? It does seem that it are not all worms that were tested in A when I’m counting? In C. the Native microbiota YA, there seem to be two groups, a group that does as well as the E. coli group and a group that performs poorly. Is this related to Figure 3?

 

Line 191: How many animals were counted?

 

Line 192: E. coli not in italics.

Author Response

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Author Response File: Author Response.pdf

Reviewer 2 Report

The manuscript by Slowinski et al. report the effect of different bacteria on life history traits of C. elegans. In particular, they find that native microbiota generally tend to induce faster
development but have lower fecundity after heat stress during adult stages. This reveals some tradeoff between early and late developmental phenotypes.

Generally, the paper is well written and the results and methods seem to be sound. However, somtimes the experiments are not clearly described and I have some concerns regarding the interpretation of the results.

 

Major concerns:

l. 130
"Together, these results indicate that nutritional value alone is not sufficient to support worm development (kanamycin-killed E. coli)" I do not think, this conclusion is justified. If the treatment of bacteria would lead to the production of certain bacterial toxins, or the antibiotics could not be washed away completely, the inhibitted/delayed development could be due to the toxic effect. To test if living bacteria release growth promoting signals into the environment, one could add bacteria-free supernatants of CEnt1 to nematodes growing on PFA-killed bacteria and test if this leads to accelerated growth. Alternatively, E. coli could release signals/toxins that inhibit growth. If that is the case, supernatants of E. coli or dead E. coli could actually inhibit growth. I would really like to see what happens if PFA-killed EC is added to PFA-killed CEnt1.

 

l. 169 - 172
I wonder if the increased susceptibilty to heat-shock of worms that have been exposed to the complex microbiotas actually represents decreased heat stress resistance or a shifted temperature optimum. If the exposure to complex microbiota shifts the temperature optimum to lower temperatures then comparing the same heat treatment between E. coli and Native microbiota culture worms is not a fair comparison and therefore not valid. If an altered temperature optimum would explain the lower fecundity, then I would expect that the native microbiota should lead to higher fecundity under a cold stress condition.

l. 181 - 183
It is not clear to me, what was the set up of the two separate experiments that showed the opposite effect on development (Figure 3). Are these just biological replicates of the experiments from Figure 2 or was the experimental set up different? If these were just replicates, I wonder what the source of the variability of the experimental outcome is. Is that stochastic noise (priority effects) during the colonisation of native microbiota? Also, if these are biological replicates of the same experiment, what does that indicate for the reproducibility of the the finding that native microbiota lead to faster development?

 

l. 209 - 211
I am not totally sure but I think, the authors interpret here "the absence of evidence" as "the evidence of absence" To support their hypothesis, the faster developing condition (in this case E. coli) should have a significantly reduced fecundity. This is the case in Fig 3B but not in Fig 3A. Thus, this does not look like conclusive evidence to me.

Minor comments:

l. 101
"Controls confirmed that neither PFA-killed nor kanamycin-killed bacteria could grow on plates." Maybe the authors could rephrase this sentence to make clear how the controls were done? e.g. "As a control, we seeded plates with PFA-treated or kanamycin-treated bacteria. These plates were checked after xx minutes/hours to confirm that no PFA-killed nor kanamycin-killed bacteria could grow on plates."

l. 118 "Work by others expanded on this theme [14,20]"  - I am not sure what to learn from this statement. I would suggest that if these studies [14,20] revealed findings that are relevant for the current manuscript, the authors should reiterate these findings and put the citation. If that is not the case, I would suggest to delete the whole sentence as it does not contain any relevant information.

l. 146 Fig 1
maybe the letters denoting the significance classes should be added to the legend, this
would make it easier to assign letters to growth curves. e.g. it is unclear in Fig1B if the letter a represents Libe Cent1 and KAN-killed EC.

l. 146 Fig 1
It would be nice to extend the x-axis scale in panel until 80 hours, to make the three panels more comparable (even if the experiment stopped at 50h).

l. 153 the legend of Fig 1 (C) suggests that one representative experiment out of three biological replicates was shown. Are panels 1 and 2 based on single replicates? That it is fine but it would be nice if that would be explicitly stated.

l. 163
"We focused on worm resistance to mild heat stress (31 C, 6 h), which commonly tracks longevity [26-28]." I am sorry but "resistance to mild heat stress" tracks "resistance to mild heat stress" not longevity! References [26-28] seem to show that these traits may coincide. This should be rephrased e.g. "We focused on worm resistance to mild heat stress (31 C, 6 h). Thermotolerance has previously been found to coincide with extended lifespan and thus could be used as proxy for it [26-28]."

l. 190 Figure 3
The usage of correlation is a bit misleading, I would prefer to use "inverse relationship" instead.

l. 192 E.coli -> italic

 

 

 

Author Response

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Author Response File: Author Response.pdf

Round 2

Reviewer 1 Report

Dear authors,

 

I am satisfied with how my comments were addressed.

Author Response

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Author Response File: Author Response.docx

Reviewer 2 Report

The authors did a good job of addressing most of my previous comments (Reviewer 2). However, they could not remove my uncertainty about the interpretation of two of their results. Therefore, two major concerns still persist and I would recommend to address these by changing the strength of their conclusions. The manuscript is still interesting enough to be publishable, even if there exist multiple explanations for their results.

Major concerns:

Previous comment (Reviewer 2): l. 130: "Together, these results indicate that nutritional value alone is not sufficient to support worm development (kanamycin-killed E. coli)" I do not think, this conclusion is justified. If the treatment of bacteria would lead to the production of certain bacterial toxins, or the antibiotics could not be washed
away completely, the inhibitted/delayed development could be due to the toxic effect. To test if living bacteria release growth promoting signals into the environment, one could add bacteria-free supernatants of CEnt1 to nematodes growing on PFA-killed bacteria and test if this leads to accelerated growth. Alternatively, E. coli could release signals/toxins that inhibit growth. If that is the case, supernatants of E. coli or dead E. coli could actually inhibit growth. I would really like to see what happens if PFA-killed EC is added to PFA-killed CEnt1

Author's response: Kanamycin is a protein synthesis inhibitor so production of new proteins should not be possible. Furthermore, it is not toxic at all to worms. We clarify this point to Methods. Regarding potential toxicity of E. coli, decades of work with E. coli OP50 showed no indication of toxicity.While not directly addressing the reviewer’s request for an experiment, previous work in the lab (accompanying Berg et al. 2016, Frontiers in Microbiology; although I believe that the graph was ultimately not included in the manuscript) included a large scale experiment where live E. coli and CEent1 were
mixed in different ratios. This experiment demonstrated that CEent1 accelerated host development even at a 1:1000 or 1:10 6 dilution. These results support our suggestion that CEent1 accelerates development better than it supports the possibility raised by the reviewer, that E. coli toxicity slows development. We attach the graph below (2.1 refers to CEent1, N2 is the wildtype C. elegans strains; each column represents ~100
worms). However, we don’t think that this experiment belongs in the current manuscript.

My response: I would like to thank the authors for providing access to the results of the mixing experiments. These result indeed support the E. coli is not inhibitting growth. Nevertheless, I am still not convinced that the experiments with dead bacteria are conclusive to make such a strong statement. Why do the two treatments lead to vastly different outcomes (line 128-132, Fig 1a,b)? The fact that worms can grow on E. coli does not mean that it is not toxic (or contains toxic metabolites). Decades of work with worms grown on E. coli OP50 have only shown how little we understand this system. This is exemplified by the fact that 40% of C. elegans genes are still without any functional annotation (Petersen et al. 2015, PMID: 25577479). The statement that there is no indication that E. coli OP50 is not toxic, is simply a lie. Just, to give one example, the work by the Walhout lab have shown that the E. coli diet leads to a vitamin B12 deficiency. One function of Vitamin B12 is to prevent the accumulation of propionic acid, which is toxic (Watson et al. 2014 PMID: 28898637). As it stands, the only way for me to recomend
acceptance of this paper is if the authors change the following statements:

l. 132-134

"Together, these results INDICATE that nutritional value alone is not sufficient to support worm development  (kanamycin-killed E. coli), suggesting that worm development additionally requires bacterially-provided signals."

should be changed to

"Together, these results SUGGEST that nutritional value alone is not sufficient to support worm development (kanamycin-killed E. coli) AND that worm development additionally requires bacterially-provided signals."

or an equivalent phrasing should be used.

 

Previous comment: l. 169 – 172 I wonder if the increased susceptibilty to heat-shock of worms that have been exposed to the complex microbiotas actually represents decreased heat stress resistance or a shifted temperature optimum. If the exposure to complex microbiota shifts the temperature optimum to lower temperatures then comparing the same heat treatment between E. coli and Native microbiota culture worms is not a fair
comparison and therefore not valid. If an altered temperature optimum would explain the lower fecundity, then I would expect that the native microbiota should lead to higher fecundity under a cold stress condition.

Author's response: We don’t think that this interpretation is likely to be true: the fecundity in normal temperature is identical for worms raised on E. coli and on the native microbiome. This suggests that we don’t have a shift of a curve, leaving heat stress sensitivity a more likely possibility.

My response: The fact that the authors think, an alternative interpretation is unlikely does not rule out the possibility that it could be true. Therefore, the authors' preferred interpretation is also not certain and consequently, no strong conclusion can be drawn. In addition, the fact that no significant difference could be detected at benign temperatures (Figure 2B) does not indicate that "the fecundity in normal temperature is identical for worms raised on E. coli and on the native microbiome." This is exactly the "the absence of evidence" as "the evidence of absence" problem. Looking carefully at these plots, the median fecundity of worms grown on native microbiota is consistently higher for L4 and young adults, even if the difference is not significant. But what would now happen if the authors repeat the experiment at slightly lower temperature? If the same trend would exist and the difference would be significant, this would support an altered temperature optimum. As the authors cannot rule out the possibility of a shifted temperature optimum, the following sentences should be changed

l. 177-179
"This INDICATED that faster development on complex microbiotas was associated with reduced fecundity, but only when heat stress was further applied, suggesting a microbiota-dependent trade-off between fast development and heat stress resistance."

"This SUGGESTS that faster development on complex microbiotas was associated with reduced fecundity, but only when heat stress was further applied, IMPLYING a microbiota-dependent trade-off between fast development and heat stress resistance."

or an equivalent phrasing should be used.

 

l. 207-209
"However, our results DEMONSTRATE that benefits manifested in one life history trait, attributed to interactions with microbes in an animal’s natural environment, can trade-off with another life history trait"

-->

"However, our results IMPLY that benefits manifested in one life history trait, attributed to interactions with microbes in an animal’s natural environment, can trade-off with another life history trait"

 

l. 213-214
"Thus, our results INDICATE a trade-off between an early life
history trait (development), and a late-life history trait (adult stress resistance)."

"Thus, our results SUPPORT a trade-off between an early life
history trait (development), and a late-life history trait (adult stress resistance)."

 

Author Response

Please see the attachment

Author Response File: Author Response.docx