Variability of plasmid fitness effects contributes to plasmid persistence in bacterial communities

Plasmid persistence in bacterial populations is strongly influenced by the fitness effects associated with plasmid carriage. However, plasmid fitness effects in wild-type bacterial hosts remain largely unexplored. In this study, we determined the fitness effects of the major antibiotic resistance plasmid pOXA-48_K8 in wild-type, ecologically compatible enterobacterial isolates from the human gut microbiota. Our results show that although pOXA-48_K8 produced an overall reduction in bacterial fitness, it produced small effects in most bacterial hosts, and even beneficial effects in several isolates. Moreover, genomic results showed a link between pOXA-48_K8 fitness effects and bacterial phylogeny, helping to explain plasmid epidemiology. Incorporating our fitness results into a simple population dynamics model revealed a new set of conditions for plasmid stability in bacterial communities, with plasmid persistence increasing with bacterial diversity and becoming less dependent on conjugation. These results help to explain the high prevalence of plasmids in the greatly diverse natural microbial communities.

In this manuscript Alonso-del Valle and colleagues studied the distribution of plasmid fitness effect in natural bacterial strains isolated from the human gut. A common perception in microbiology is that plasmid acquisition incures a fitness cost to the host. Nonetheless, plasmids are common in nature (including the hospital environment, which is the topic of research in this manuscript). Several studies published in recent years (also in Nat Comm) aimed to reconcile plasmid ubiquity with their possible fitness effect on the host. Here, using a unique collection of natural isolates, the authors quantified the fitness effect of plasmid carriage in diverse strains of two speices: E. coli and K. pneumoniae. The model plasdmid in this study is a 'natural' conjugative plasmid of medium size (ca. 60Kb) and encodes for antibiotics resistance. Their results, overall, show that the plasmid has very often a negligible fitness effect on the hosing isolate. Additionally, the author supplement their study with simulations of plasmid persistence in a mixed population depending on the plasmid fitness and transfer frequency. The results are clearly presented and the manuscript is well written. This study supplies a realistic view on the fitness effect (and hence evolutionary implications) of plasmid acquisition and as such, I expect that it will be interesting for Nat Comm readership and highly popular in the fields of microbial ecology and evolution (and likely also medical microbiology).
Note: I do not have the necessary background to evaluate the modelling approach. The results section of the part is accessible and well explained. Still, I would try to connect it even better to the experimental part.

Comments
For using ANOVA one has to validate that the data fits the assumptions of that test. Specifically the test of normal distribution has to be performed and P value reported. Figure 4b shows that only two of the tested isolates do not contain any plasmdis. This should be mentioned the text. I guess from the figure that there is no correlation between the fitness effect and the native plasmid content. Is that true?
The calibration of the fitness effect of pGBC is a neat solution (lines 499+). Im missing some data here on the experimental design. Is the calculation performed with averaging or per replicate (i.e., with replicates also for the pGBC+/wt competition)?
The sequences are uploaded to NCBI, albeit, only as SRA, which makes them inaccessible for the common user. I would ask the authors to upload the assembeled and annotated draft genomes to make them available to the community.
Suggestions I see no reason to prefer the term 'quasi neutral' over neutral. I would replace the first with the latter.
The figures quality could improved -specifically the phylogenetic trees should be plotted with thicker branches and larger OTU font size.   For the correlation with the phylogenetic position -I would actually try to calculate a simple spearmen correlation between the delta fitness and the pairwise distances that were used to construct the phylogenetic tree. A scatter plot of that data might be interesting (and revealing). This is an interesting study that expands our knowledge of plasmid-host interactions. The study comproses two parts, first experimental measurement of the DFE of a plasmid across a clinical strain collection; second a model implementing these data into a population ecology model of plasmid dynamics.
The first part of the paper represents a lot of careful experimental work. The main result, that the DFE ranges from -20% to +20% fitness effects for a single plasmid is interesting. Moreover, these fitness effects seem to explain the distributionof the plasmid in the =clinic at least in Klebsiella. Given the plasmid came from Klebsiella originally, this stronger singal compared to E. coli is perhaps not unexpected. The work is clearly explained and thorough, with clear and informative figures and a simple but robust statistical analysis. I was at first concerned by the use of J53 in some of the competitions, but it is clear from the methods that this was carefully validated. A very nice job! The model expands on the classical framework of Levin and colleagues. The main finding is that allowing for a distribution of fitness effects expands the parameter space in which plasmids survive. Moreover, plasmid stability scales positively with host diversity only when plasmid fitness effects can vary between hosts. The first result here is trivial and expected from Levin type models: in essence, if plasmids can sometimes be beneficial, then they can survive... The second result is more interesting and not immediately obvious from Levin style models.
The modelling is limited to the parameters derived from the experiments. This is fine in so far as it goes but does limit the concluclusions to low cost plasmids. I think that the modelling shown in the paper should be expanded a bit to allows for a fuller exploration of parameter space e.g. I would expect that the effect of DFE is strongly dependent on the mean fitness effect as well as the variance, in that with larger costs the effect of the DFE diminishes because fewer plasmi-host interactions fall into the neutral/beneficial zone? For such high cost plasmids therefore, conjugation would be the main mechanism of maintenance Overall I like the paper but feel that it is a bit oversold. The DFE perhaps "explains" persistence of low cost /nearly neutral plasmids, but is unlikely to explain it for other plasmid-host systems where the mean effect is a large cost and few/none of th e associations fall into the neutral/benficial FE space, for these persistence will still be "explained" by conjugation. I would like to see the title and some of the conclusions toned down a bit, and for an expanded set of conditions to be modelled, and appropriate caveats added to explain when DFE will matter most Reviewer #3 (Remarks to the Author): The manuscript by Alonso-del Valle et al. investigates the persistence of the antibiotic resistance plasmid pOXA-48 in an experimental setting using isolates of enterobacteria from the human gut. The authors examine the effect of pOXA-48 on the fitness of plasmid hosting strains. They find that while they often detect a fitness reduction in the host strains, in many isolates the plasmid does not have a negative impact on the host and may even be beneficial to the bacterial host. Using this data for a population model, the authors show that bacterial diversity may be more important than conjugation for the persistence of plasmids in natural bacterial communities. The study shows interesting aspects of plasmid persistence in a quasi-natural setting. I believe their results represents an important addition the field of plasmid evolution and antibiotic resistance spread. Nevertheless, their study lacks certain depth and further investigation in the observed fitness effects of plasmids in natural clinical isolates is missing (especially in the genomics part). Furthermore, a major issue is the connection of the experimental part with the modelling part.
Major comments 1. The authors state in line 81-84 "Our criteria were to select (i) pOXA-48-free isolates, to avoid selecting clones in which compensatory evolution had already reduced plasmid-associated costs; (ii) isolates from the most frequent pOXA-48-carrying species, K. pneumoniae and Escherichia coli; and (iii) strains isolated from patients located in wards in which pOXA-48-carrying enterobacteria were commonly reported". How can the authors be sure that the plasmid was not present in the strain before? According to their sampling scheme, it seems almost likely that the strains are commonly exposed to the plasmid. An analysis of the plasmid-carrying genomes versus plasmid-free genomes could help to answer that question. In any way, the authors cannot be sure that the plasmid never "saw" the host strain and the observed results may be very well explained by the evolutionary history of certain isolates.
2. In line 119-120 and Figure 2a statistics are missing and should be reported.
3. Is there a fitness effect of the plasmid pBGC carrying GFP in the natural isolates? GFP may have an effect on the fitness of the cells/culture. The authors should clarify this point in the main text as it may majorly influence the relative fitness calculation. Do the authors have a comparison of the fitness effect in the commonly used E.coli strain MG1655? Would be interesting to see the fitness effect in a potentially less closely related strain (for comparison). 6. I am not convinced of the relevance of comparing the results of the current study to another comparative study. The results of the Vogwill & maclean study are collected from very different experiments, especially laboratory settings. The authors should consider omitting this section. 7. Figure 4 shows very interesting results and represents an interesting approach to interpret the presented fitness data. The authors analyze the genomes of the host strains as well as their mobile elements in association with the observed fitness effects. They observe that some closely related isolates are negatively affected by the plasmid while others are positively affected. This finding fits to the observation of the plasmid spread shown in ref. 31. Such results could hint to compensatory evolution in some strains that often encounter the plasmid in a natural setting. The authors should clarify this point. The isolates that are negatively affected also have a 'high' plasmid load. Could some of these plasmids affect pOXA stability or cost? Furthermore, did the authors check for genetic signatures in plasmid-carrying strains that might be found also in plasmid-free strains (data from ref. 31)? This may help to further explain the differences in the plasmid fitness cost distribution.
8. Unfortunately, I am not an expert in mathematical models and cannot judge the conducted mathematical model in this study. Nonetheless, a major issue is the connection of the experimental part with the modeling part that is currently lacking. The authors need to justify the connection of the two parts.
Minor comments -The authors should consider to increase the font size in figures 1-4 (as it is very hard to read!).
-line 130: The authors state that they were unable to introduce pBGC into eight of the isolates and used E. coli strain J53 carrying the pBGC vector. The author need to mark (e.g., in figure 2b) which were these strains as it could have significant effect on the calculation of the relative fitness.
Reviewer #4 (Remarks to the Author): This study first shows that the fitness effect of one particular, medically relevant plasmid varies greatly between strains of two medically relevant species known to carry this plasmid in clinical settings. The authors then assessed the effect of the variation in plasmid cost on plasmid persistence in bacterial communities whose members show such a diversity in plasmid fitness effects. The study questions are very significant and the results are important, especially of the beneficial effect of the plasmid on some strains, but there are also several points of concern, and the novelty is a bit overstated.
1. I am afraid the term "distribution of fitness effects (DFE)" is already being used extensively in evolution and population genetics with a slightly different meaning (DFE of new mutations). As the authors point out in their first sentence of the Discussion, "The DFE for new mutations is a central concept in genetics and evolutionary biology, with implications ranging from population adaptation rates to complex human diseases". DFE refers however to the distribution of fitness effects of a mutation within a population of cells. This concept and its measurement have been at the center of key debates in evolutionary biology for at least 15 years and the authors are not citing much of this literature. I do not think DFE should be used in the context the authors are trying to use it -which is differences in fitness effects (of a plasmid) among different strains of either E. coli or K. pneumoniae that have multiple genetic differences and form a community (the term they use in the second part of their Results). This will only cause confusion in the literature, especially given the broad nature of this journal. The strains in the manuscript have multiple genetic differences that are not fully described, are too numerous to clearly determine how the strains are related to each other (mutational steps), and certainly not causally linked to the effect of the plasmid on host fitness. Even in future studies these differences are likely too numerous to allow for easy identification of which genomic differences (=genetic context) explain the heterogeneity in plasmid fitness cost. The Distribution of Fitness effects involves the estimation of the total fitness effects of mutations as resulting from the sum of all the individual gene effects (i.e. the direct genotype to phenotype map) and the consideration of the so-called environmental effects, or the effects of the genetic context in which the gene of interest is expressed. These cannot be distinguished here. The authors could use the terms heterogeneity or variability, but not this population genetics term DFE.  (refs 23, 25), with the only difference that the main experimentally measured parameter was plasmid persistence (=stability), and plasmid fitness effects were measured (and estimated through modeling) for only a subset of the total number of strains. In principle it showed the same: that the fitness cost of a plasmid to its hostand therefore the long-term persistence -is very variable between hosts, even closely related strains. Moreover, a decade later Kottara et al (2018 -FEMS ME, 94 (1)) showed something very similar (from the abstract: "These data confirm that plasmid stability is dependent upon the specific genetic interaction of the plasmid and host chromosome rather than being a property of plasmids alone, and moreover imply that MGE dynamics in diverse natural communities are likely to be complex and driven by a subset of species capable of stably maintaining plasmids that would then act as hubs of HGT"). Therefore the following statements on L. 59-60 and L. 351 are not correct in my opinion: "In this study, we provide the first description of the distribution of fitness effects (DFE) of a plasmid in wild-type bacterial hosts", and "but the DFE of a plasmid in multiple, ecologically compatible bacterial hosts had not been reported before". The hosts used in the studies mentioned above were environmental strains, and in some of these studies several strains were from the same habitat. They all received the plasmid naturally by conjugation, just like in this study, and most were from an environment where that type of plasmid is frequently found, just like here for pOXA-48 .
If anything, this study shows that variability (i.e. stochastic population dynamics) is an essential component to better understand plasmid persistence, but demonstrating that concept in combination with experimental results is not new (see for instance abstracts in Ponciano et al. (2007) and De Gelder et al. (2007): "Also, we present a stochastic model in which the relative fitness of the plasmid-free cells was modeled as a random variable affected by an environmental process using a hidden Markov model (HMM). Extensive simulations showed that the estimates from the proposed model are nearly unbiased. Likelihood-ratio tests showed that the dynamics of plasmid persistence are strongly dependent on the host type. Accounting for stochasticity was necessary to explain four of seven time-series data sets, thus confirming that plasmid persistence needs to be understood as a stochastic process" and "Remarkably, a large variation in the stability of pB10 in different strains was found, even between strains within the same genus or species. ... "The findings of this study demonstrate that the ability of a so-called 'BHR' plasmid to persist in a bacterial population is influenced by strain-specific traits, ...").
And then there is the study/studies by Hall et al (see comment 10).
All this takes away from the novelty of this study, even though it is going further than these older studies. It aims at assessing the effect of the variation in plasmid cost on plasmid persistence in bacterial communities whose members show a diversity in plasmid fitness effects. The study would be more novel if this concept would be the focus of this new study, and not the observation that there is variation between strains.
3. L. 49: "First, most experimental reports of fitness costs have studied arbitrary associations between plasmids and laboratory bacterial strains 7,24." This relates to comment 2 above. I don't agree with this statement. I don't know why previously published plasmid-host associations would seem 'arbitrary'. Many strains used to assess plasmid fitness cost and its amelioration over time have been rather recent environmental isolates (see also some of the papers form the Brockhurst group). They were relevant plasmid-host associations and 'natural bacterial hosts' (L. 51). Maybe there were 'arbitrary' lab strains in these two references 7 and 24 but not in all studies published so far. 4. The statistical estimation of the ODE model parameters via the Bayesian analysis is not validated, nor sufficiently explained. From the description of the methods and the results, it is not clear that the authors fully understand how to present their statistical analyses. It seems that the reaches and limitations of their analyses are not fully understood. MCMC is not, for instance, an inferential paradigm. The authors seem to confuse statistical models with an inferential approach (Bayesian or frequentist, for example). The authors should look at statistical/model oriented papers in ecology journals to see examples of how to fit population dynamics models. Furthermore, the authors do not provide evidence that the statistical method properly estimated the model parameters. The model is not checked, there is no comparison with the priors, and it is not shown how specifying the different priors affects the results. The authors should consider taking a simulating approach and simulate data sets of the exact same dimensionality as the observed data sets instead of simulating much longer data sets? Useful papers on how to validate Bayesian analyses are by A. Gelman and C.R. Shalizi ("Philosophy and the practice of Bayesian Statistics") and Lele, S.R. (2020) (Consequences of lack of parameterization invariance of noninformative Bayesian analysis for wildlife management: Survival of San Joaquin kit fox and declines in amphibian populations. Front. Ecol. Evol. 7: 501. doi: 10.3389/fevo).
There are at least two other important concerns with the modeling portion of this manuscript: 1) When this paper is published and the data and code shared as stated in the last line of the manuscript, every analysis should be repeatable by any student or faculty interested in the topic. The diagnostic tests for their parameter estimation process should be transparent and made available as a supplement.
2) The authors should demonstrate unequivocally that the model parameters are uniquely identifiable and that the data they have is sufficient to tease apart the model parameter estimates. They should also demonstrate that their inferences are robust to model assumptions and repeatable under different prior parameterizations. The recent ecological literature has seen a flurry of papers presenting similar analyses but seldom practitioners stop to document the robustness of their inferences. 5. 'Neutral' (L. 213, 315, 374 ..) and 'quasi-neutral': (L. 23, 346, 355). While the data, and especially the variation in the data, supports the null hypothesis that there is no plasmid cost in several strains, I am not sure I would call these plasmids having a neutral effect (and quasi-neutral is not defined here). The method is simply not sensitive enough to detect very small fitness costs (or benefits) that may nonetheless have a long-term impact on the population dynamics of the organism. No detectable fitness effect is not the same as no fitness effect. That is, the absence of evidence is not evidence of absence.
6. Fig. S1 shows growth curves for transconjugants/plasmid-free strains, as does Fig 2. But where is the correction for the carriage of the plasmid with the fluorescent protein? That effect can differ between strains, yet it seems to be published separately: Fig. S10 shows the effect of that small plasmid separately, and there clearly is an effect in many strains. It is not sufficient to say "Note that the fitness effects of pBGC did not correlate with those form pOXA-48". Even when there is not statistically significant correlation, for some strains the reported fitness effect of the pOXA plasmid may have been confounded by the presence of this plasmid, possibly leading to erroneous conclusions about how many strains were benefiting from or inhibited in their growth by the plasmid! The fitness effect of the pOXA plasmids should be corrected for the fitness effect of this small plasmid (in Figure 2, 3). From what I understand this was not done. (The authors have shown themselves in the past that there may be poorly understood interactions between co-residing plasmids, and these interactions may differ between host backgrounds). 7. L. 41-46: Another factor that tends to be forgotten: the fact that some plasmids have extremely high fidelity in their partitioning and on top of that the ability to inhibit the growth of plasmid-free segregants (psk). I honestly think that there is not such a strong paradox anymore when all these elements are considered.
8. It was not clear how the variability of the growth curve data (known to be quite noisy) from the 5 replicates per strain were considered in Fig. 1. Only one point per strain is shown but what is the variability within a strain? All the replicates should be plotted. 9. Title ("The distribution of plasmid fitness effects EXPLAINS plasmid persistence in bacterial communities") AND L. 28 ("Our results provide a simple and general explanation for plasmid persistence in natural bacterial communities"). This sounds as the findings from this study are the ONLY explanation of plasmid persistence in bacterial communities. This should be toned down a bit in my opinion. "Diversity of plasmid fitness effects contributes to plasmid persistence in bacterial communities" would be more accurate as a title. 10. I missed discussion of the papers by James Hall and others (e.g. their source-sink paper in PNAS) that addressed the fate of a plasmid in a two-species community.
Minor Comments: 1. L. 21, L. 139, elsewhere: What are "ecologically compatible" strains? 2. L. 25 "set of conditions for plasmid stability in bacterial communities, with plasmid persistence increasing with bacterial diversity and becoming less dependent on conjugation". This relates to the Results on L 311...: I understand that this implies that because some bacteria are better hosts than others, the more diversity of strains, the higher the probability that a plasmid will be retained in that community. However, what if that strain (or strains) is/are a minority in the community? I think your approach assumes equal relative abundance for each type of host (=perfect evenness), but that is typically not the case ?
3. L. 177: The conclusion on Figure 3 ("Note that relative fitness values are normally distributed") seems misleading to the reader: As the data for E coli and Klebsiella are stacked, the distribution looks indeed normal, but when looking at both species separately, the Klebsiella data do not seem as normally distributed as the E coli data. Is it OK to lump the data? 4. Fig. 4: It wasn't clear if the authors looked at correlation between fitness effect of the pOX plasmid and the families of other plasmids in the strains (inner circles). Are these data used at all in the analyses or interpretations? If not, why are they shown? 5. Fig. 4: I would recommend using another color scale than red-green, given there are many color-blind readers.
6. L. 307: "allowing fitness effects to vary between members of the population". I think the authors mean 'community' here, as they defined above (L. 284: "To explore how plasmid stability is affected by increasing community complexity" 7. L. 376: "phylogeny might influence fitness compatibility between plasmids and bacteria at the clonal level,". This should be reworded. I think the authors are trying to say that (as yet unknown) genetic differences between strains of the same species can explain differences in plasmid fitness cost. The word 'phylogeny' seems a bit too vague here. The next sentence is great though.
8. It would be helpful to some readers to indicate that pOXA-48 is an IncL/M-plasmid.
We would like to thank the reviewers for their helpful criticisms, which have allowed us to increase the quality of the manuscript. We have substantially revised the manuscript following the reviewers' suggestions, which we found particularly useful. The changes are highlighted in yellow in the revised manuscript.
We have introduced several significant changes that we briefly highlight here: -We have tone down our statements and conclusions throughout the manuscript, and we have also modified the tittle. Moreover, we now highlight the effect of the variability of fitness effects in plasmid stability in complex polyclonal bacterial populations as the main novelty of the work.
-We have modified the figures to increase size and quality. We have included 5 new supplementary figures to address the reviewers' requests.
-We improved the connection between the experimental part and the mathematical model, and we have expanded the model to explore a broader parameter space.
-We have extended the genomic analysis to investigate the correlation between pOXA-48_K8 fitness effects and the native plasmid content of the wild type strains.
-We have extensively improved the controls of model parameterization and we include a file with the diagnostic plots of the MCMC algorithm for all strains used in this study (Supplementary File 1).
We provide a point-by-point response to the reviewers' comments here:

REVIEWER COMMENTS
Reviewer #1 (Remarks to the Author): In this manuscript Alonso-del Valle and colleagues studied the distribution of plasmid fitness effect in natural bacterial strains isolated from the human gut. A common perception in microbiology is that plasmid acquisition incurs a fitness cost to the host. Nonetheless, plasmids are common in nature (including the hospital environment, which is the topic of research in this manuscript). Several studies published in recent years (also in Nat Comm) aimed to reconcile plasmid ubiquity with their possible fitness effect on the host.
Here, using a unique collection of natural isolates, the authors quantified the fitness effect of plasmid carriage in diverse strains of two species: E. coli and K. pneumoniae. The model plasmid in this study is a 'natural' conjugative plasmid of medium size (ca. 60Kb) and encodes for antibiotics resistance. Their results, overall, show that the plasmid has very often a negligible fitness effect on the hosing isolate. Additionally, the authors supplement their study with simulations of plasmid persistence in a mixed population depending on the plasmid fitness and transfer frequency. The results are clearly presented and the manuscript is well written. This study supplies a realistic view on the fitness effect (and hence evolutionary implications) of plasmid acquisition and as such, I expect that it will be interesting for Nat Comm readership and highly popular in the fields of microbial ecology and evolution (and likely also medical microbiology).
We thank the reviewer for these comments.
Note: I do not have the necessary background to evaluate the modelling approach. The results section of the part is accessible and well explained. Still, I would try to connect it even better to the experimental part.
In the new version of the manuscript, we included several modifications in Results sections to provide a better connection between the modelling section and the experimental part (lines 266-273, lines 297-304, lines 333-334).

Comments
For using ANOVA one has to validate that the data fits the assumptions of that test. Specifically the test of normal distribution has to be performed and P value reported.  We thank the reviewer for this insightful comment. We mention now that only 2 isolates do not carry any plasmids (lines 258-259). We have performed new analyses to investigate the potential correlation between the native plasmid content and the fitness effects of plasmid pOXA-48_K8. A simple correlation between the number of different plasmids in the host bacterium and pOXA-48 fitness effects produced no significant results: Scatter plots illustrating the correlation analyses between the number of plasmids and the relative fitness of pOXA-48_K8-carrying isolates. An estimate of the Pearson correlation coefficient is provided within each plot, along with its p-value. The regression lines and confidence intervals at 0.95 (shadow) are represented.
However, we have performed a much more detailed analysis trying to link the plasmid profile (absence/presence of plasmids belonging to each plasmid family) with pOXA-48 fitness effects for Klebsiella spp. isolates, where the LIPA analysis revealed a significant association between the accessory genome and pOXA-48_K8 fitness effects for a subset of isolates. We performed a Factor Analysis of Mixed Data (FAMD), which allows analysing datasets containing both quantitative and qualitative variables (new Supplementary Figure 6). Interestingly, this analysis revealed that the presence of plasmids belonging to the IncFIA or IncH1B families, and the absence of plasmids belonging to the IncFIB family, were associated with high pOXA-48_K8 costs in Klebsiella spp. isolates. We have included these results in the manuscript (lines 228-235), and in a new Supplementary Figure (Supplementary Figure 6).
The calibration of the fitness effect of pGBC is a neat solution (lines 499+). Im missing some data here on the experimental design. Is the calculation performed with averaging or per replicate (i.e., with replicates also for the pGBC+/wt competition)?
We have tried to improve the explanation in the methods section. In the previous section we explained: "We The sequences are uploaded to NCBI, albeit, only as SRA, which makes them inaccessible for the common user. I would ask the authors to upload the assembeled and annotated draft genomes to make them available to the community.
We agree with the reviewer. We have now uploaded all the assembled and annotated draft genomes to the NCBI under the same accession code (BioProject ID PRJNA641166, https://www.ncbi.nlm.nih.gov/sra/PRJNA641166). We include this information in the methods section (lines 599-600), and in the data availability statement (lines 746-747). The BioSample Accession codes of these genomes are SAMN15344961 to SAMN15345007. We scheduled these sequences for immediate release, although it may take GenBank a few weeks to make the annotated genomes available and provide the final accession numbers.
Suggestions I see no reason to prefer the term 'quasi neutral' over neutral. I would replace the first with the latter.
We thank the reviewer for this suggestion. We have removed quasi-neutral from the paper, and we have also removed neutral, as suggested by reviewer 4.
The figures quality could improved -specifically the phylogenetic trees should be plotted with thicker branches and larger OTU font size.
We have included the changes suggested by the reviewer.  We agree with the reviewer that a CDF helps to interpret the results presented in Figure 3. Therefore, we have included insets in both panels in Figure 3 representing the CDF of the different datasets (Figure 3 and  We have clarified in the figure legend that the accessory genome tree is a gene content tree (line 255). We tried to present the fitness data as a colour gradient on the branches, but we finally decided to maintain the outer circle with the colour-code instead, because we think it is easier to interpret for the reader.
For the correlation with the phylogenetic position -I would actually try to calculate a simple spearmen correlation between the delta fitness and the pairwise distances that were used to construct the phylogenetic tree. A scatter plot of that data might be interesting (and revealing).
We thank the reviewer for this suggestion. We have followed this advice and studied these correlations. The results of these correlations are qualitatively similar to those we obtained with the phyloSignal R package 1 , which include different tools specifically designed to identify statistical dependence between a given continuous trait (relative fitness) and the phylogenetic tree of the taxa from which the trait is measured. we observed a small signal for the core genome of E. coli isolates, but non-significant after all.
Moreover, we also performed the same analysis for each different clone; the correlation between the delta fitness and phylogenetic distance compared to the remaining clones of the same genus: Scatter plots illustrating the correlation analyses between the delta fitness and the pairwise distance obtained from the phylogenetic trees and dendrograms of the core genome and the accessory genome respectively for each isolate of Escherichia coli and Klebsiella spp. An estimate of the Pearson correlation coefficient is provided within each plot, along with its p-value. The regression lines and confidence intervals at 0.95 (shadow) are represented. The confidence intervals shadowed in red indicates a p-value < 0.05.
Interestingly, in these analyses we obtained similar results to those obtained with the Local Indicator of Phylogenetic Association (LIPA) analysis, which is probably not that surprising. Specifically, we found significant correlations both for accessory and core genomic content for K. pneumoniae ST1427 isolates (and also for the accessory genome in Kpn19, which we did not detect with LIPA).
In summary, we consider that our analysis using the phylosignal R package and LIPA are quite robust, because these tools are specifically designed to look for associations of traits with phylogeny. Therefore, we  We have included this information in the figure legend (line 380).

Reviewer #2 (Remarks to the Author):
This is an interesting study that expands our knowledge of plasmid-host interactions. The study comprises two parts, first experimental measurement of the DFE of a plasmid across a clinical strain collection; second a model implementing these data into a population ecology model of plasmid dynamics.
The first part of the paper represents a lot of careful experimental work. The main result, that the DFE ranges from -20% to +20% fitness effects for a single plasmid is interesting. Moreover, these fitness effects seem to explain the distribution of the plasmid in the clinic at least in Klebsiella. Given the plasmid came from Klebsiella originally, this stronger singal compared to E. coli is perhaps not unexpected. The work is clearly explained and thorough, with clear and informative figures and a simple but robust statistical analysis. I was at first concerned by the use of J53 in some of the competitions, but it is clear from the methods that this was carefully validated. A very nice job! We thank the reviewer for these comments.
The model expands on the classical framework of Levin and colleagues. The main finding is that allowing for a distribution of fitness effects expands the parameter space in which plasmids survive. Moreover, plasmid stability scales positively with host diversity only when plasmid fitness effects can vary between hosts. The first result here is trivial and expected from Levin type models: in essence, if plasmids can sometimes be beneficial, then they can survive... The second result is more interesting and not immediately obvious from Levin style models.
The modelling is limited to the parameters derived from the experiments. This is fine in so far as it goes but does limit the conclusions to low cost plasmids. I think that the modelling shown in the paper should be expanded a bit to allows for a fuller exploration of parameter space e.g. I would expect that the effect of DFE is strongly dependent on the mean fitness effect as well as the variance, in that with larger costs the effect of the DFE diminishes because fewer plasmid-host interactions fall into the neutral/beneficial zone? For such high cost plasmids therefore, conjugation would be the main mechanism of maintenance.
We thank the reviewer for this constructive suggestion. We have followed the reviewer's advice and we have extended the parameter space analysed in our model to consider a wider range of average fitness effects.
Specifically we have determined the conjugation threshold that positively selects for plasmids in the population as a function of the average fitness cost and assuming a range of variances of fitness effects (including zero variance). Interestingly, and as predicted by the reviewer, the effect of the heterogeneity in fitness effects is more important for plasmids producing a small cost, while plasmids producing a large cost depend more dramatically on a high conjugation rate. We have included this information in the manuscript (lines 297-304), and also as a new panel in Figure 5 (5d, lines 323-331).
Overall I like the paper but feel that it is a bit oversold. The DFE perhaps "explains" persistence of low cost /nearly neutral plasmids, but is unlikely to explain it for other plasmid-host systems where the mean effect is a large cost and few/none of th e associations fall into the neutral/benficial FE space, for these persistence will still be "explained" by conjugation. I would like to see the title and some of the conclusions toned down a bit, and for an expanded set of conditions to be modelled, and appropriate caveats added to explain when DFE will matter most.
We have toned down our statements and conclusions throughout the manuscript. We have also modified the tittle of the paper to tone down the message. We specified now that the variation in fitness effects would be most relevant for plasmids producing on average a small fitness reduction, while conjugation will still be the Furthermore, a major issue is the connection of the experimental part with the modelling part.
We thank the reviewer for the comments. In the new version of the manuscript, we provide a better connection between the experimental part and the modelling part (lines 266-273, lines 297-304, lines 333-334). We also performed a deeper analysis connecting native plasmid content with pOXA-48_K8 fitness effects (see response to question #7 below).
Major comments 1. The authors state in line 81-84 "Our criteria were to select (i) pOXA-48-free isolates, to avoid selecting clones in which compensatory evolution had already reduced plasmid-associated costs; (ii) isolates from the most frequent pOXA-48-carrying species, K. pneumoniae and Escherichia coli; and (iii) strains isolated from patients located in wards in which pOXA-48-carrying enterobacteria were commonly reported". How can the authors be sure that the plasmid was not present in the strain before? According to their sampling scheme, it seems almost likely that the strains are commonly exposed to the plasmid. An analysis of the plasmidcarrying genomes versus plasmid-free genomes could help to answer that question. In any way, the authors cannot be sure that the plasmid never "saw" the host strain and the observed results may be very well explained by the evolutionary history of certain isolates.
We agree with the reviewer. We cannot be 100% sure that the plasmid has not been present in the strain before. We selected pOXA-48-free isolates recovered from patients with no record of previous colonisation One important characteristic of pBGC is that GFP expression is inducible, so during the overnight competition GFP is repressed, we only induce its expression when we are about to measure the cell ratios in the flow cytometer. Therefore, the effect of GFP expression in the outcome of the competition is limited (this data is presented in the methods section, lines 133-134, lines 526-528, and we have added a new explanatory sentence in lines 547-548).
We measured the fitness effects of plasmid pBGC in the natural isolates, as presented in the previous version of the manuscript (Supplementary Figure 13) The fact that each independent growth curve parameter present a weak (but significant) correlation with the relative fitness values (w) is probably not that surprising, since w is affected by all of these parameters simultaneously, so its is maybe normal that none of them will explain all the variation in w independently.
However, what we think is very significant is the fact that when we used the exact same growth curves data Our intention with this comparison is to highlight the importance of using "ecologically compatible", environmentally co-occurring, plasmids and bacteria when trying to understand the actual fitness effects produced by plasmids in their natural bacterial hosts. In this context, the comparison seem relevant to us since the works analysed in the meta-analyses include mostly combinations of plasmids and bacteria of very diverse origins (lines 183-184), in contrast to the ones in our study. Therefore, we would prefer to keep this section as part of the manuscript, because we believe that it helps to make the point that plasmid fitness effects are likely influenced by the ecological compatibility between plasmids and their bacterial hosts.
7. Figure 4 shows very interesting results and represents an interesting approach to interpret the presented fitness data. The authors analyze the genomes of the host strains as well as their mobile elements in association with the observed fitness effects. They observe that some closely related isolates are negatively affected by the plasmid while others are positively affected. This finding fits to the observation of the plasmid spread shown in ref. 31. Such results could hint to compensatory evolution in some strains that often encounter the plasmid in a natural setting. The authors should clarify this point. The isolates that are negatively affected also have a 'high' plasmid load. Could some of these plasmids affect pOXA stability or cost?
We thank the reviewer for this suggestion. We have performed now a much more detailed analysis trying to link the plasmid profile (absence/presence of plasmids belonging to each plasmid family) with pOXA-48_K8 fitness effects for Klebsiella spp. isolates, where the LIPA analysis revealed a significant association between the accessory genome and pOXA-48_K8 fitness effects for a subset of isolates. We performed a This is a really interesting suggestion. This is an analysis that we are planning on doing in the near future, but if we want to do a comprehensive analysis we need to increase the sample size of plasmid-free isolates with sequenced genomes (and ideally measure pOXA-48_K8 fitness effects in those isolates too). We are planning on focusing on Klebsiella pneumoniae ST11, which is the most common host for pOXA-48-like plasmids in our hospital (and in many other hospitals in Spain/Europe). We have a large collection of pOXA-48-carrying ST11 from the hospital, but we need to increase the sample size of pOXA-48-free ST11 isolates (in this study we only included 4 K. pneumoniae ST11 isolates). We believe that using plasmid-free/plasmidcarrying isolates form the same ST will dramatically increase the power of a GWAS-type analysis. However, we believe that this particular analysis goes beyond the scope of the present paper.
8. Unfortunately, I am not an expert in mathematical models and cannot judge the conducted mathematical model in this study. Nonetheless, a major issue is the connection of the experimental part with the modeling part that is currently lacking. The authors need to justify the connection of the two parts.
In the new version of the manuscript, we included several modifications in Results sections to provide a better connection between the modelling section and the experimental part (lines 266-273, lines 297-304, lines 333-334).
Minor comments -The authors should consider to increase the font size in figures 1-4 (as it is very hard to read!).
We have re-edited all the figures and increase size and quality. We also include the figures as independent files to facilitate their inspection.
-line 130: The authors state that they were unable to introduce pBGC into eight of the isolates and used E.
coli strain J53 carrying the pBGC vector. The author need to mark (e.g., in figure 2b) which were these strains as it could have significant effect on the calculation of the relative fitness.
The names of these strains were indicated in the methods section on the competition assays (lines 566-567), but we have also included this information in the section of "Construction of pBGC, a GFP-expressing nonmobilizable plasmid" (line 534). We have indicated the competitions that were performed using E. coli J53/pBGC instead of the wild-type clone with pBGC in Figure 2b This study first shows that the fitness effect of one particular, medically relevant plasmid varies greatly between strains of two medically relevant species known to carry this plasmid in clinical settings. The authors then assessed the effect of the variation in plasmid cost on plasmid persistence in bacterial communities whose members show such a diversity in plasmid fitness effects. The study questions are very significant and the results are important, especially of the beneficial effect of the plasmid on some strains, but there are also several points of concern, and the novelty is a bit overstated.
We thank the reviewer for the comments. "These data confirm that plasmid stability is dependent upon the specific genetic interaction of the plasmid and host chromosome rather than being a property of plasmids alone, and moreover imply that MGE dynamics in diverse natural communities are likely to be complex and driven by a subset of species capable of stably maintaining plasmids that would then act as hubs of HGT").
Therefore the following statements on L. 59-60 and L. 351 are not correct in my opinion: "In this study, we provide the first description of the distribution of fitness effects (DFE) of a plasmid in wild-type bacterial hosts", and "but the DFE of a plasmid in multiple, ecologically compatible bacterial hosts had not been reported before". The hosts used in the studies mentioned above were environmental strains, and in some of these studies several strains were from the same habitat. They all received the plasmid naturally by conjugation, just like in this study, and most were from an environment where that type of plasmid is frequently found, just like here for pOXA-48.
If anything, this study shows that variability (i.e. stochastic population dynamics) is an essential component to better understand plasmid persistence, but demonstrating that concept in combination with experimental showed that the estimates from the proposed model are nearly unbiased. Likelihood-ratio tests showed that the dynamics of plasmid persistence are strongly dependent on the host type. Accounting for stochasticity was necessary to explain four of seven time-series data sets, thus confirming that plasmid persistence needs to be understood as a stochastic process" and "Remarkably, a large variation in the stability of pB10 in different strains was found, even between strains within the same genus or species. ... "The findings of this study demonstrate that the ability of a so-called 'BHR' plasmid to persist in a bacterial population is influenced by strain-specific traits, ...").
And then there is the study/studies by Hall et al (see comment 10).
All this takes away from the novelty of this study, even though it is going further than these older studies. It aims at assessing the effect of the variation in plasmid cost on plasmid persistence in bacterial communities whose members show a diversity in plasmid fitness effects. The study would be more novel if this concept would be the focus of this new study, and not the observation that there is variation between strains.
We thank the reviewer for this comment. We agree that in the previous version of the manuscript we We agree with the reviewer that "arbitrary" was not the best word to use in this context. We have changed this statement. We now explain most experimental reports of fitness costs have studied associations between plasmids and bacterial strains from different ecological origins (lines 48-50). We think that this claim is true, and we provide many references now to support it [4][5][6][7][8][9][10][11][12][13]  There are at least two other important concerns with the modeling portion of this manuscript: 1) When this paper is published and the data and code shared as stated in the last line of the manuscript, every analysis should be repeatable by any student or faculty interested in the topic. The diagnostic tests for their parameter estimation process should be transparent and made available as a supplement.
We agree with the reviewer on the importance of repeatability and transparency in science. We have 2) The authors should demonstrate unequivocally that the model parameters are uniquely identifiable and that the data they have is sufficient to tease apart the model parameter estimates. They should also demonstrate that their inferences are robust to model assumptions and repeatable under different prior parameterizations. The recent ecological literature has seen a flurry of papers presenting similar analyses but seldom practitioners stop to document the robustness of their inferences.
We thank the reviewer for this comment. The estimability and robustness of the MCMC algorithm used to parametrize a simple Monod model to OD data was established in a previous study 5 . In any case, we have included in the new version of this manuscript the results of a data-cloning method used to assess parameter identifyability 17,18 . Figures in Supplementary File 1 (panels f-g) show that, as the number of data clones increases, the marginal posterior distribution of both growth kinetic parameters, specific affinity (V max /K m ) and cell efficiency (ρ), converges to a multivariate normal distribution with a mean equal to the maximum likelihood estimate, thus suggesting that both parameters are uniquely identifiable. To assess the robustness of the maximum likelihood estimates when considering different priors, we repeated the parametrization of all strains for uniform, beta, gamma and lognormal distributions, obtaining similar posterior distributions, as illustrated in in Supplementary File 1 (panels c-d). An ANOVA test allowed us to reject the null hypothesis that there are significant differences in estimates when considering different priors (p-value>0.05), therefore concluding that the MCMC algorithm is repeatable under different prior parametrizations 19 .
5. 'Neutral' (L. 213, 315, 374 ..) and 'quasi-neutral': (L. 23, 346, 355). While the data, and especially the variation in the data, supports the null hypothesis that there is no plasmid cost in several strains, I am not sure I would call these plasmids having a neutral effect (and quasi-neutral is not defined here). The method is simply not sensitive enough to detect very small fitness costs (or benefits) that may nonetheless have a long-term impact on the population dynamics of the organism. No detectable fitness effect is not the same as no fitness effect. That is, the absence of evidence is not evidence of absence.
We thank the reviewer for this comment. We do not use either "neutral" or "quasi-neutral" in the new version of the manuscript. Instead, we explain that the plasmid produces moderate effects in most of the bacterial hosts tested (lines 122, 302).
6. Fig. S1 shows growth curves for transconjugants/plasmid-free strains, as does Fig 2. But where is the correction for the carriage of the plasmid with the fluorescent protein?
In growth curves, the bacterial isolates are cultivated as pure cultures (only one clone per growth curve, not two). The growth curve data was obtained from pure cultures of pOXA-48_K8-free and pOXA-48_K8carrying wild type isolates. Therefore, there is no correction to be done here, because none of those isolates express GFP. On the other hand, in the competition assays two different clones compete in the same culture. We used the pBGC-carrying (GFP-expressing once induced with arabinose) wild type isolates for the competition assays, and in this case the data was corrected to remove the effect of pBGC, as we explained in the methods sections (lines 535-584).
That effect can differ between strains, yet it seems to be published separately: Fig. S10 shows the effect of that small plasmid separately, and there clearly is an effect in many strains. It is not sufficient to say "Note that the fitness effects of pBGC did not correlate with those form pOXA-48".
Again, the fitness effects of pBGC are accounted for, and the relative fitness is calculated removing the effect of pBGC (see lines 558-564). Please see also response to the third comment form Reviewer #1 and to comment number 3 from Reviewer #3.
Even when there is not statistically significant correlation, for some strains the reported fitness effect of the pOXA plasmid may have been confounded by the presence of this plasmid, possibly leading to erroneous conclusions about how many strains were benefiting from or inhibited in their growth by the plasmid! The fitness effect of the pOXA plasmids should be corrected for the fitness effect of this small plasmid (in Figure   2, 3). From what I understand this was not done. (The authors have shownthemselves in the past that there may be poorly understood interactions between co-residing plasmids, and these interactions may differ between host backgrounds).
This correction had been done and is explained in detail in the methods section.
7. L. 41-46: Another factor that tends to be forgotten: the fact that some plasmids have extremely high fidelity in their partitioning and on top of that the ability to inhibit the growth of plasmid-free segregants (psk). I honestly think that there is not such a strong paradox anymore when all these elements are considered.
We thank the reviewer for this comment. pOXA-48_K8 carries in fact a PSK system (PemI/PemK). However, as we explained in the methods section (lines 487-493), despite this system in 7 out of the 50 isolates we found a very small % of plasmid-free colonies after propagating cultures in LB with no antibiotic selection (two consecutive days, 1:10,000 dilution) and plating cultures on LB agar. Moreover, using CRISPR-Cas9 technology we are able to cure pOXA-48 form wild-type isolates (data from a different project, not published), and this would be impossible if the PSK were completely effective. Therefore, these systems are not 100% infallible. In the introduction of the paper we just reflect the state of the art in the field, which includes the "plasmid paradox".
8. It was not clear how the variability of the growth curve data (known to be quite noisy) from the 5 replicates per strain were considered in Fig. 1. Only one point per strain is shown but what is the variability within a strain? All the replicates should be plotted.
In supplementary Figure 1 we represented the curves of each isolate, including the 95% confidence intervals. In the new version of the manuscript we also include now a new Supplementary Figure (2) with all the independent replicates for ODmax, AUC and µ max values, as suggested by the reviewer. In any case, the results from the growth curves are complemented with the results from the competition assays, which provide a direct measure of relative fitness.
9. Title ("The distribution of plasmid fitness effects EXPLAINS plasmid persistence in bacterial communities") AND L. 28 ("Our results provide a simple and general explanation for plasmid persistence in natural bacterial communities"). This sounds as the findings from this study are the ONLY explanation of plasmid persistence in bacterial communities. This should be toned down a bit in my opinion. "Diversity of plasmid fitness effects contributes to plasmid persistence in bacterial communities" would be more accurate as a title.
We agree with the reviewer and we have changed the tittle following her/his suggestion to "Variability of plasmid fitness effects contributes to plasmid persistence in bacterial communities". We have also changed the statement in line 28. 10. I missed discussion of the papers by James Hall and others (e.g. their source-sink paper in PNAS) that addressed the fate of a plasmid in a two-species community.