Field of Science

Harsh reviews of the postdoc's DNA uptake manuscript

We finally (after two months) got the reviews back for the postdoc's manuscript about DNA uptake bias.    It's a rejection -  the reviews were quite negative.  The first reviewer was very unfair; they didn't find any fault with the methods or data or analysis, but they attacked our brief discussion of the functional evolutionary context of uptake bias.  This is all too common for my papers.  The reviewer is so hostile to the idea that bacteria might take up DNA for food that they don't focus on the science.  Because the paper was rejected we don't get to do an official response to the reviews, so I'm relieving my frustration by responding to them here.

Reviewer #1: 

Suitable Quality?: No 
Sufficient General Interest?: No 
Conclusions Justified?: No 
Clearly Written?: No 
Procedures Described?: Yes 

The compelling topic of DNA uptake mediated by uptake signal sequences (USS) in Haemophilus influenzae transformation is addressed. Mell et al utilize Illumina-based deep sequencing of DNA recovered after uptake in transformation to study the uptake specificity of a Haemophilus influenzae strain. They re-confirm previous reports (Maughan, 2010), documenting the importance of the GCGG core in the USS, by using a new method. The experimental data is sound and the analysis of sequencing reads and degenerate USS is solid. New data are represented by the detection of interaction effects between individual USS positions, although this part constitutes only a small part of the manuscript presented. The Authors then attempt to inform ongoing debates on the function and evolution of the DNA uptake machinery, making suggestions which are not supported by their data. This is a particular concern due to the extensive self-referencing and simultaneous exclusion of references central to the

All of this is peripheral to the main focus of the paper, which is the nature of the uptake bias, not the function of DNA uptake.  The reviewer thinks the data and analysis are just fine, but wants the paper to be rejected anyway.

General comments: 

The paper by Mell et al contains ample general statements beyond the scope of the study, which are not supported by the data. 

Yeah, in the Discussion we try to put the results in their evolutionary and functional context.

Many of these statements are based on old models for DNA uptake in transformation and for the evolution of USS, that never were documented. 

???Old models for DNA uptake in transformation?  Meaning for the mechanism?  There aren't any old models, and ours is the only rigorous model that's been presented.  The old 'model' for the evolution of USS, that cells take up DNA for sex, are just hand-waving.

The extensive referencing of own publications (17% of references), particularly in regard to molecular drive (see below), and the lack of reference to reports in the field conveying contradicting views, weaken the validity of the manuscript. 

We cite 8 of our own papers and 35 papers from other groups.  That doesn't seem unreasonable, especially since we're the only group with recent papers on the topic.

Specific comments: 

P3 L13 Why is Bakkali PNAS 2007 not referenced here? Why not Chu et al., Artif Life 2005 or Chu et al., J Theor Biol 2006? 

We could indeed have cited these guys, and will in the revised version.  

P3 L16-20 The Authors fail to mention/acknowledge that if "not evolved by natural selection for optimizing gene expression" (which is obvious since they are agents for DNA uptake), USS may have evolved by natural selection for being beneficial in securing uptake of homologous DNA. 

Here's what we wrote:  Unlike transcription factor binding sites, uptake sequences do not evolve by natural selection for optimizing gene expression, but instead are thought to accumulate as an indirect consequence of uptake bias because they replace chromosomal sequences by homologous recombination (4).  We have addressed the issue of whether USS evolve by selection for uptake benefits in ref 4 and elsewhere.  Nobody else has presented any solid arguments against this.

Competent bacterial species have evolved several adaptations to favour homologous DNA in transformation and only overlooking substantial contributions in the literature on the subject (e.g. the entire bibliography on pneumoococci) allows for an illusive sequence of logic. 

Does this refer to the pneumococcal work on mismatch repair in recombination?  On the bizarre notion that cells kill themselves to provide DNA for their neighbours?  The reviewer simply asserts the existence of 'adaptations to favour homologous DNA in transformation' - we're the only group that thinks such assertions should be treated as testable hypotheses.

The Authors then go on to advocate molecular drive (or rather some unspecified form of molecular drive) as the mechanism behind the evolution of USS. 

Not 'unspecified'; we've published a rigorous and detailed model.

This is highly controversial. The concept of molecular drive in this context may only make sense in its neglect of the influence of natural selection as the evolutionary mechanism responsible for the evolution of transformation. Since molecular drive in general represents a downsized view
on evolution, this theory has had its rise and fall in popularity and is today a largely outdated concept (as seen in the publication record referring to the subject). 

What?  Molecular drive only makes sense in the neglect of the influence of natural selection?  We have shown that molecular drive is the null hypothesis, able to explain uptake sequences without any need to invoke natural selection.  The onus is now on others to provide evidence that (i) natural selection is needed to explain the observations, and (ii) natural selection is able to explain the observations.  

P3 L21-23: References 1 and 5 do not demonstrate that "Sequence specificity acts at the initial steps of DNA uptake, when DNA fragments are bound and transported across the Gram-negative outer membrane, pulled through type II secretin pores by the retraction of type IV pseudopili", neither does reference 37. 

Aarrghh!  This old canard!  It's absolutely clear from the experiments in this paper and many previous ones that uptake specificity acts at transport of DNA across the outer membrane.  In these experiments cells are given radioactively labelled DNA fragments containing either a USS or a control sequence.  The USS-containing fragments become protected from added DNase and pellet with the cells, and the control fragments stay in the culture medium.  This stupid assertion keeps coming up in reviews of our papers, probably from the same reviewer every time... 

P4 L18-19: "Since USS and DUS are thought to have accumulated due to biased uptake,.." has never been shown. 

We've shown that biased uptake plus recombination is sufficient to drive USS and DUS into genomes, using modeling.

Perhaps we could someday do a demonstration experiment:  1. Find a place in the chromosome where there's a mediocre match to the uptake consensus (a poor USS).  2.  Synthesize a degenerate pool of fragments containing better and worse versions of this USS.  3. Ligate this into a long fragment with the flanking chromosomal DNA, so we have a pool of long fragments, all identical except for the USS degeneracy.  4.  Incubate competent cells with this pool. 5.  Sequence this segment of the genomes of these cells, to show that they have become enriched for better versions of this USS.  We'd want to do this without selecting for acquisition of the fragment.  Maybe do several cycles of incubation and recovery?  We could use sxy-1 or murE749 cells to get high frequencies of transformation.  If I genuinely thought that this experiment would convince our critics, I'd do it.  But they would probably say that the outcome was obvious, as it indeed is.

P5 L 3 and P 15 L16: Statements such as "..DNA's intrinsic stiffness, charge and length." , "..pulling stiff charged DNA molecules through the narrow secretin pore."and "..physical constraints imposed by stiff highly charged DNA" attempt to describe restrictions in the uptake of DNA by making suggestions which are not supported by their data. 

Yes, this is the Introduction and Discussion, not the Results.

P5 L6-9: This statement does not comply with molecular drive since adaptations per definition cannot evolve by that mechanism, and the Authors must make up their mind: Natural selection or molecular drive? 

Huh?  That's not what we said.  We said that preferential uptake is widely assumed to be an adaptation, and contrasted that assumption with our model.

P5 l1-12 ..deep sequencing to provide a detailed characterization of H. infleunzae's uptake specificity." - deep sequencing of what? 

Of the recovered DNA fragments of course, as spelled out in the previous paragraph.

P6 L9 Reference to Bakkali PNAS 2004 is missing 


P 14 L20 and on: Why are the nice data presented in Results not systematically discussed here? Instead, a general discussion on uptake-specificity systems and their (co-)evolution is presented, which is way beyond the main scope of the study. 

We'll include a bit more discussion of the data in the revised version, but it's so self-evident that there's not really much to discuss.

P14 L21-23 and on. Why are multiple speculations not supported by the data, presented here? The evolutionary concept presented is flawed. 

This is the Discussion...

P14 L23-P15 L2: The Authors do not seem to appreciate that the breaking up of genetic associations itself can be beneficial and hence subject to natural selection (for review, see: Otto and Lonormand, Nature 2002; Otto 2008.). It is also a misunderstanding that it is the amount of USS that is directly favourable as stated, but rather the sequence quality of the surrounding allele(s). 

The authors certainly do appreciate this, since we have published several mathematical modeling papers investigating whether selection for recombination benefits can be strong enough to select for genes causing natural transformation.  Bottom line:  it probably can't.  We rarely mention this work in our experimental papers because we don't expect the reviewers to understand them.

P15 L5-13: The question of the evolutionary benefit of being a picky eater is still causing a problem for the reasons mentioned above. The entire evolutionary constellation of molecular drive and USS not being an adaptation is entirely built on the weak and over-interpreted analyses in reference 4, which is cited more than 10 times in the manuscript, in order to attempt to present a consistent view on evolution. The Authors aim at separating the evolution of USS from that of transformation itself, which proves difficult since the advantages of acquiring homologous DNA in nature are extremely well documented. 

Sure.  The advantages of winning the lottery are extremely well documented too, but that doesn't mean that buying lottery tickets is a good investment.

P15 L 19-21: No data presented refers to the claims regarding deformation and kinking of DNA. 

This is the Discussion.  In the revision we'll mention DNA's persistence length and give a reference.

Reviewer #2: 

Suitable Quality?: No 
Sufficient General Interest?: No 
Conclusions Justified?: No 
Clearly Written?: Yes 
Procedures Described?: Yes 

The prokaryote Haemophilus influenzae is naturally competent and the transport of DNA across the membrane is done through a secretion system derived from T2SS/T4P which requires a sequence signal known as the uptake signal sequence (USS). The manuscript describes an analysis of this uptake signal sequence. This has been done several times before. First, it was done experimentally following pioneering works in 70's. This was later redone by using genome sequences following the sequencing of the genome in 1995. 

No, as we take pains to point out, the analysis of genome sequences does not tell us about the bias of the uptake machinery.  One of the goals of our paper is to test the hypothesis that the genomic sequences accurately reflect the uptake bias.

Here, the authors have used a combination of the experimental approach and mass-sequencing to re-analyze the question. They generate a large pool of degenerated USS and compare this input pool with the one found in the periplasm of the cell. The difference between the two should provide the information on the bias of the secretion system for the USS. The scale of this experimental approach is novel for this problem, yet the results are not very different. The only systematic difference between the USS definition in the previous and this work relates with the average preference of the positions that are outside of the core of the signal. Overall, the authors find fewer preferences than expected, i.e. weaker signal for USS. Hence, genomic scans might have over-inflated frequencies of the consensus at these positions or this work may have done the inverse. 

The uptake machinery is indeed related to Type 2 secretion systems, but it seems silly to call it a secretion system...  It's hard to see how our experiments could have over-inflated the uptake bias, given that what we did was directly measure the effect of uptake.

1) This paper is often opinionated in an odd way. The difference between the USS obtained by the experiment and the ones observed from genome scans can be due to a number of issues, notably: other biases in subsequent steps, genome constraints and non-linear effects at transport. 

The first is dismissed in one single sentence " The discrepancy is unlikely to be caused by undetected sequence biases at later steps of natural transformation (translocation of ssDNA to the cytoplasm and recombination into the chromosome). Such biases no doubt exist, but they are unlikely to amplify the specific biases of the uptake machinery. " 

There's nothing wrong with using a single clear sentence to explain why a possible explanation doesn't apply.

The second is dismissed in the same way: " A similar argument applies to constraints acting at the level of genome evolution; natural selection certainly will have acted on uptake sequences that arose in coding regions or in positions where they could act as transcriptional terminators, but this is unlikely to have specifically strengthened the apparently weak uptake biases of the outer core and T-tracts." 

So, for both arguments the authors sustain that these effects certainly exist but needn't be taken into account. In fact, there are a number of published reasons why these effects must be taken into account. It is well known that USSs accumulate in certain regions of the genome more than in others (for example, Smith, Res Mic, 99). In particular, they tend to accumulate more than expected in intergenic regions (three times more than expected in Haemophilus) and be part of rho-independent terminators. This means the genomic scans will fetch the bias associated with USS, but also the bias of intergenic regions (AT richness) and sequences flanking the core structure of the rho-independent terminator (stretches of T after the terminator and A before the terminator if it is a bi-directional terminator). This is the exact difference between figs 4 A and fig4 B and could thus explain the discrepancies. Therefore, the argument of the authors that the differences between USS in this work and genomic scans are not due to any of the two first causes is not convincing. It must be seriously sustained in some way. 

This is a valid point.  Years ago I did some analysis of how terminator function and coding functions affect the genomic USS motif (see this post especially).  This analysis never got published, but the results are very significant in the context of the uptake analysis and we might want to include them in our revised manuscript. 

Finally, the author's argument is that there are interactions between bases and this means the consensus needs not be as strong as thought. Characteristically, the sentence is " A better explanation may be that the uptake motif model described above is compromised by its assumption that each position contributes independently to uptake, i.e. that interaction effects between positions make no contribution. ". The reasons why this is a "better explanation" are not stated in the text. And I'm afraid I don't understand this point. If the consensus in the genome reflects only the incoming DNA and the filtering at the outer membrane (as the authors state) then the two consensus should be similar with or without interaction effects because the genomic consensus is the simple result of the initial consensus. 

Doesn't this contradict the previous concern that other factors might contribute to the genomic consensus?

This is of utmost importance for the discussion of this article, because the deviation between the genomic USS motif and the one identified by the authors is the only biological novelty presented. 

Not true.

2) All positions in the motif are less biased in the current experiment than in the genome scans. This also includes the core positions that are well known to be important biologically. Can't this discrepancy be simply the results of experimental error in DNA extraction? If there is contamination between extracellular (or membrane-bound) DNA and periplasmic DNA one expects to have a mixture of OM-filtered and non-OM-filtered sequences and therefore a weaker signal. Exactly, the observed result. Also, standard population genetics predicts that the genomic patterns should be *weaker* not stronger than import biases in a selfish model because selection occurs at the entry point. Genomic sequences will endure drift and thus USS should be weaker not stronger in genomes relative to OM-filtered sequenced. That motifs are stronger in genomes suggests selection for the best motifs for the bacterial benefit, not a selfish drive. 

The reviewer is mistakenly assuming that the absolute information contents (in bits) of the two motifs are comparable.  They're not because the input sequences were derived in very different ways.  We had cut from the manuscript the sentence pointing this out; clearly we need to restore it.

3) The manuscript has a couple of errors that make its reading difficult. 

In the legend of Fig 4 the panels A and B seem inverted relative to the description given in the text. 

Oops, yes.

The first formula in page 19 should have + not -. The original formula is log2(N)-(-sum(slog2(s)) (see Crooks, Genome Res, 04) which makes log2(N)+sum(slog2(s)), thus sum(slog2(s*N)). My calculations suggest the calculations of the authors are correct and that just the formula is wrong, but this should be checked. 

No, the formula and calculations are both correct.

In page 15, l16 the authors indicate that it might be an important mechanistic problem to pass the DNA through the narrow secretin pore. No reference is given for this. The family of Secretins is known to be extremely flexible. Secretin pores can transport folded proteins and even entire phage particles. Some evidence should be given (at least a reference) that pore size would be a problem to transport DNA. 

Here we'll point out the persistence length, which greatly exceeds any reasonable estimate of the pore flexibility.

4) The analysis of interactions seems to neglect the effect that these positions are not independent within the design of the experiment. Because the experiment aims at defining regions with a certain degeneracy this should mean that if one position matches the consensus the other position under comparison is *less* likely to match the consensus simply by the design of the method (because degeneracy must be in some positions and it is not at the focal position). The significance of this effect should be checked since interactions are not very strong. 

No.  We didn't force every fragment to have the same number of mismatches (nor could we have).  Our supplementary data (analysis of the sequencing of the input DNA fragments) shows that mismatches were randomly distributed among the input fragments.

5) The exact differences between the two USS are difficult to assess by the use entropic measures. The problem would be much more appropriately analyzed by using classical population genetics of selective processes, because that's exactly the process at hand if you replace natural selection by transport system selection. 

Huh?  I don't see any way to treat this as a population genetics problem.  We've certainly done lots of population genetics in other papers, on other aspects of transformation and USS evolution, but I don't think it can be applied here.


  1. Ah, the old death by a thousand (BS) cuts. Been there and it stinks.

  2. Hope you're feeling better now. I really like open access. I like your blog. I like science in general... but I understand it to be a human endeavor, fraught with human foibles. You missed the Bakkali ref., Reviewer 1 caught it. You switched panels in Fig 4, Reviewer 2 caught that one. This doesn't mean your paper is bad, but it does speak to the value of review.

    But what I really want to contribute today is a reaction I had when reading one of your comments to Reviewer 1. You said:

    We rarely mention this work in our experimental papers because we don't expect the reviewers to understand them.

    Is that how you really feel? You actually compose serious scientific communication with an expectation that a certain population of supposedly peer scientists will not understand mathematical modeling?

    1. Yup. It's not that they're incapable of understanding the modeling results, but they won't take the trouble and the context of the paper doesn't justify providing a pre-digested explanation.

  3. Hi! I saw your mention of the idea that microbes might take up DNA just for the purpose of "eating" it and thought you might be interested in the following paper, in which we hypothesize that indeed microbes might be especially interested in getting the P out of the DNA they "eat".

    Souza, V., L. Eguiarte, J. Siefert, and J.J. Elser. 2008. Microbial endemism: does nutrient limitation enhance speciation? Nature Reviews Microbiology 6: 559-564.


    Jim Elser

  4. Hi Rosie,

    This is a completely unrelated point, and I apologize in advance for being a stickler when you're already (justifiably) frustrated about something more important, but I'm curious about your thoughts on this:


    1. Aarrghh! Why does this stupid article keep tormenting me! Every time I read Slate I see messages saying that my 'Facebook friends' liked this article, even though I never use Facebook.

      I always put two spaces after a period. I think it does make text easier to read. The only reason I would stop is if fonts changed to include more space with the period itself.

    2. Even though stupid Blogger insists on removing my double spaces...

    3. Sorry! I just wondered if you genuinely thought it looked better. Now I know! (But I disagree.)

  5. Sounds like BAD SCIENCE to me. Maybe you can publish it in an open access journal.


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