Now I see how to give the Innovation section a narrative, and accomplish other things too. The key was to see it as a way to reinforce the rest of the proposal.
The proposal begins with a Specific Aims page, which provides a summary of what I propose to do and why. This is followed by several pages of Significance, which provide a more detailed explanation of what the problems are that this work will help address. After the Innovation section comes the Approach, where I spell out each Specific Aim in detail, emphasizing how it will be accomplished.
In an old-style proposal, the Specific Aims page would be called the Summary, the Significance section would be Background, the Approach would be Methods, and the place now occupied by Innovation would be where the Specific Aims were listed, connecting the problems raised in the Background with the solutions described in the Methods.
There's no reason that the Innovation section can't also accomplish what a traditional Specific Aims section accomplished. So mine will begin with "I am proposing three Specific Aims, each innovative in both concept and strategy." Then I will have a paragraph for each Aim in turn, explaining how our approach differs from previous approaches and why it is the best solution to its problem. In doing this I will also be giving the reader an overview of the Aims both in the context of the broad Significance they've just read and in the context of the detailed Approach sections they're about to read.
Field of Science
-
-
Change of address1 year ago in Variety of Life
-
Change of address1 year ago in Catalogue of Organisms
-
-
Earth Day: Pogo and our responsibility1 year ago in Doc Madhattan
Are we innovative yet?
NIH wants its applicants to use somewhere between half a page and a full page of the 12-page proposal to explain how their proposals are innovative. Here's NIH's instructions:
The field is recombination (in its broad sense, everything from the molecular mechanisms to the evolutionary consequences), and we're going to fully characterize recombination between related strains. That is, we're going to find out (i) the properties of the recombination tracts and (ii) the probabilities of recombination for ~all differences between the strains. This will be done using deep sequencing of single and pooled recombinant genmes, and will give an extremely comprehensive picture of recombination across the ~40,000 snps and 300 indels and rearrangements that distinguish these two strains. Then we're going to use recombination to map genes responsible for the very low transformation frequency of one of the strains.
I've been making lists of things that are innovative about what we propose, but what's lacking is a coherent narrative that ties them together. So I'm going to just start listing them here and see if a narrative comes together...
- Explain how the application challenges and seeks to shift current research or clinical practice paradigms.
- Describe any novel theoretical concepts, approaches, methodologies, instrumentation, or intervention(s) to be developed or used and any advantage gained.
- Explain any refinements, improvements, or new applications.
- Significance is why the work is important to do.
- Innovation is why the work is different from (better than) what has been done before.
- Definition of innovation: a new device or process resulting from study & experimentation; the act of introducing something new.
- How will research in your field change as a result of your work?
- Demonstrate the potential gains are not merely incremental.
- Explain why concepts & methods are novel to one field or novel in a broad sense (or both).
- Summarize (sans detailed data) novel findings to be presented as preliminary results in Approach
- Focus on innovation in study design & outcomes
The field is recombination (in its broad sense, everything from the molecular mechanisms to the evolutionary consequences), and we're going to fully characterize recombination between related strains. That is, we're going to find out (i) the properties of the recombination tracts and (ii) the probabilities of recombination for ~all differences between the strains. This will be done using deep sequencing of single and pooled recombinant genmes, and will give an extremely comprehensive picture of recombination across the ~40,000 snps and 300 indels and rearrangements that distinguish these two strains. Then we're going to use recombination to map genes responsible for the very low transformation frequency of one of the strains.
I've been making lists of things that are innovative about what we propose, but what's lacking is a coherent narrative that ties them together. So I'm going to just start listing them here and see if a narrative comes together...
- This will be the first time that all of the recombination of a single recombinant genome (from a single transformation event) has been identified for any organism. And we're going to do it many times (50? 100?). Maybe include actual numbers - how many recombination tracts do we expect to characterize? how many breakpoints? Relate to how many actual recombination tracts have already been characterized (I'd have to dig into the literature...)?
- By using deep sequencing to measure the frequency of recombination at tens of thousands of SNPs and indels we will characterize the full spectrum of sequence factors affecting recombination. The scale will be unprecedented. How many SNP-conversion events do we expect to detect? How many indel-conversion events?
- We are breaking down the previously necessary tradeoff between high resolution and broad scope. Deep sequencing of tine genomes lets us have it all!
- We will develop new analytical tools, to analyze recombinant genomes.
- Nobody else is focusing on the causes of the poor transformability of many strains of 'transformable' species.
- Will use genome sequencing of recombinants with altered transformability to identify recombination tracts carrying the responsible alleles. This may seem wasteful but is very efficient; one lane of sequencing (even without multiplexing) is likely to define a stretch of no more than 1 kb. (If the difference is a snp and not an indel - we should have done the phenotyping! This is a pitfall we need to write about.)
- This will (we think) be the first time that the QTL mapping methods used for eukaryote genomes are applied to bacteria. (Is this right? We need to clarify the relationship between QTL mapping and sequencing. Is anyone sequencing recombinant genomes of yeast?) They were developed out of necessity for the very large eukaryote genomes, but, now that sequencing bacterial genomes is so cheap, are very efficient when applied to bacteria that lack the sophisticated genetic tools available for E. coli and B. subtilis. We're one of the first to start using deep sequencing to replace conventional molecular biology analysis (well, 'one of' is a cop-out as I don't really know...).
about PilT
One issue we need to deal with better in our revised CIHR proposal is the identity of the H. influenzae protein that retracts its type 4 pili and/or pseudopili (short stb pili).
In the well characterized bacteria (Neisseria meningitidis, Pseudomonas aeruginosa), pilus retraction is done by the protein PilT, using energy it gets by hydrolyzing ATP. I'm just going to summarize the things I think are true, but once I've done that I'll need to read the latest papers to find the evidence for my statements, and to check what I may have gotten wrong.
The problem is that we (and others) haven't been able to identify a PilT homolog in H. influenzae, although everything we know about DNA uptake in other systems, and about the need for other proteins of the type 4 pilus system in H. influenzae, predicts that a PilT homolog should be needed to pull the DNA in (by pulling the pilus or pseudopilus in). The competence regulon (CRP-S regulon includes all of the other proteins with recognizable T4P-family signal sequences ('prepilin protease-dependent leader sequences'), but none of these are good homologs of the PilT proteins identified in other bacteria (nor of the related PilU). Nor are there recognizable PilT or PilU homologs among proteins that don't have this leader sequence.
The closest H. influenzae relative of PilT in other systems is a protein assigned as the PilB homolog. In other bacteria PilB is essential for assembly of the T4P, and we know that H. influenzae PilB is essential for DNA uptake. I'm pretty sure that PilB can't also do the job of PilT, because both proteins are ATPases. That is, in the bacteria where its function has been studied (mainly N. meningitidis and P. aeruginosa) PilB uses energy from hydrolyzing ATP to assemble pilin subunits into a pilus fiber, and PilT uses energy from hydrolyzing ATP to disassemble the pilus fiber into its subunits. From the perspective of the pilus, the PilT reaction is a reversal of the PilB reaction, but from the perspective of the ATP these are very different reactions - the energy requirement tells us that PilB will not be able to carry out pilus disassembly.
But some protein must do the work of pulling in the DNA. One possibility is that H. influenzae has a cryptic PilT homolog - maybe an ATPase that gets to the right place in the inner membrane without having a recognizable T4P targeting sequence. Another is that this function is done by an unrelated protein. I'd expect such a protein to be an ATPase,
(Here's a link to a couple of movies of P. aeruginosa cells whose pili have been made visible with fluorescent antibody. In one you can see the pili (~5 times longer than the cell) shortening, and in the other you can see the tip of an elongated pilus attaching to the slide surface at a point distant from the cell, and then shortening, pulling the cell to the attachment point.)
I can't think of any way to select or screen for a defect in pilus disassembly. This is partly because pili have not been detected on strain Rd - the group that showed pili only did this work in the clinical strain 86028-NP. That strain does detectable twitching motility under the alkaline conditions where it does produce visible pili, but it also doesn't have a PilT homolog. In fact (I think), none of the Pasteurellaceae have them. And I think that Pasteurellacean cells typically don't have type 4 pili at all. We do have a pilus-associated phenotype that we can screen for defects in - DNA uptake - and we expect a PilT mutant to be defective for this. But we have already identified lots of genes whose knockouts prevent DNA uptake and thus would be found in such a screen, so this is a lousy way to look for PilT mutants.
But let's think about this a bit more. Say there are about 25 genes needed for transformation. In principle we can do random knockouts using some well-behaved in vitro method and use transformation to put these into the chromosome (just like Gerry Barcak and Hanna Tomb did in Ham Smith's lab 20 years ago). Then we'd do a massive screen for strains that don't transform, and screen the clean nontransformers for DNA uptake, then check where the knockout was in each strain that didn't do uptake. Then we'd check out any new genes. (This strategy is looking more and more lousy with each additional screening step. If I had unlimited money I might do this, but I don't think I'd fund it over competing projects.)
An alternative plan is to start by screening the genome for proteins with ATPase motifs (Walker boxes) and then pick out the ones that have signals to target them to the inner membrane and don't have any other assigned function. If there are only a few candidates this would be reasonable, but there might be very many.
Another plan is to wait for someone else to solve the problem. Another bacterium lacking PilT is also able to retract type 4 pili - I thought it was Myxococcus, but there's a 2003 paper describing Myxococcus pilT gene - Oh, it's that Myxococcus pilT mutants can still retract their pili, though not as well as wildtype cells.
In the well characterized bacteria (Neisseria meningitidis, Pseudomonas aeruginosa), pilus retraction is done by the protein PilT, using energy it gets by hydrolyzing ATP. I'm just going to summarize the things I think are true, but once I've done that I'll need to read the latest papers to find the evidence for my statements, and to check what I may have gotten wrong.
The problem is that we (and others) haven't been able to identify a PilT homolog in H. influenzae, although everything we know about DNA uptake in other systems, and about the need for other proteins of the type 4 pilus system in H. influenzae, predicts that a PilT homolog should be needed to pull the DNA in (by pulling the pilus or pseudopilus in). The competence regulon (CRP-S regulon includes all of the other proteins with recognizable T4P-family signal sequences ('prepilin protease-dependent leader sequences'), but none of these are good homologs of the PilT proteins identified in other bacteria (nor of the related PilU). Nor are there recognizable PilT or PilU homologs among proteins that don't have this leader sequence.
The closest H. influenzae relative of PilT in other systems is a protein assigned as the PilB homolog. In other bacteria PilB is essential for assembly of the T4P, and we know that H. influenzae PilB is essential for DNA uptake. I'm pretty sure that PilB can't also do the job of PilT, because both proteins are ATPases. That is, in the bacteria where its function has been studied (mainly N. meningitidis and P. aeruginosa) PilB uses energy from hydrolyzing ATP to assemble pilin subunits into a pilus fiber, and PilT uses energy from hydrolyzing ATP to disassemble the pilus fiber into its subunits. From the perspective of the pilus, the PilT reaction is a reversal of the PilB reaction, but from the perspective of the ATP these are very different reactions - the energy requirement tells us that PilB will not be able to carry out pilus disassembly.
But some protein must do the work of pulling in the DNA. One possibility is that H. influenzae has a cryptic PilT homolog - maybe an ATPase that gets to the right place in the inner membrane without having a recognizable T4P targeting sequence. Another is that this function is done by an unrelated protein. I'd expect such a protein to be an ATPase,
(Here's a link to a couple of movies of P. aeruginosa cells whose pili have been made visible with fluorescent antibody. In one you can see the pili (~5 times longer than the cell) shortening, and in the other you can see the tip of an elongated pilus attaching to the slide surface at a point distant from the cell, and then shortening, pulling the cell to the attachment point.)
I can't think of any way to select or screen for a defect in pilus disassembly. This is partly because pili have not been detected on strain Rd - the group that showed pili only did this work in the clinical strain 86028-NP. That strain does detectable twitching motility under the alkaline conditions where it does produce visible pili, but it also doesn't have a PilT homolog. In fact (I think), none of the Pasteurellaceae have them. And I think that Pasteurellacean cells typically don't have type 4 pili at all. We do have a pilus-associated phenotype that we can screen for defects in - DNA uptake - and we expect a PilT mutant to be defective for this. But we have already identified lots of genes whose knockouts prevent DNA uptake and thus would be found in such a screen, so this is a lousy way to look for PilT mutants.
But let's think about this a bit more. Say there are about 25 genes needed for transformation. In principle we can do random knockouts using some well-behaved in vitro method and use transformation to put these into the chromosome (just like Gerry Barcak and Hanna Tomb did in Ham Smith's lab 20 years ago). Then we'd do a massive screen for strains that don't transform, and screen the clean nontransformers for DNA uptake, then check where the knockout was in each strain that didn't do uptake. Then we'd check out any new genes. (This strategy is looking more and more lousy with each additional screening step. If I had unlimited money I might do this, but I don't think I'd fund it over competing projects.)
An alternative plan is to start by screening the genome for proteins with ATPase motifs (Walker boxes) and then pick out the ones that have signals to target them to the inner membrane and don't have any other assigned function. If there are only a few candidates this would be reasonable, but there might be very many.
Another plan is to wait for someone else to solve the problem. Another bacterium lacking PilT is also able to retract type 4 pili - I thought it was Myxococcus, but there's a 2003 paper describing Myxococcus pilT gene - Oh, it's that Myxococcus pilT mutants can still retract their pili, though not as well as wildtype cells.
Articulating why us, why H. influenzae
The research associate has been going through the reviewers' comments on our unsuccessful CIHR research proposal. Much of the criticism was along the lines of 'Why should you do this when it's already been done in Neisseria*?", "Why should you do this in H. influenzae instead of Neisseria*?" and "Why should anyone try to do this, when other scientists have been unsuccessful?"
These issues are better addressed in H. influenzae. The need for a ratchet is not obvious in Neisseria, because it has long external pili. But most competent bacteria appear to pull DNA to the inner/cytoplasmic membrane with short stubby structures (pseudopili). Neisseria doesn't need long pili either, but this is only seen in mutants, whereas in H. influenzae we're studying the natural mechanism, not an aberration. We know that H. influenzae can take up circular DNAs that remain supercoiled in the periplasm, but we don't know that for Neisseria.
We will downplay testing whether competent H. influenzae have external pili. None are visible in the few published electron micrographs of competent cells, but nobody has ever specifically looked for them. We will begin with the reasonable assumption that competent cells lack external pili but will check this assumption using an anti-pilin antibody.
We may also downplay the search for the proteins that bind to DNA. It's intellectually messy work and we don't have any experience with mass-spec.
* The reviewers' emphasis on Neisseria made us wonder if one or both of them might have a Neisseria background. But I just checked the member lists for the previous two versions of this review committee, and none of them have any obvious connections to Neisseria or natural competence or pili. (These are previous committees, the membership list for our actual committee won't be released for months.) But whoever our reviewers were, they were surprisingly knowledgable!
So yesterday she took the devil's advocate position, pushing me to defend our plans. One argument we will make is that we're in a much better position than the Neisseria researchers to use uptake sequences as a tool to study the uptake mechanism. For example, we have a resource that they lack - the availability of related species with variant uptake specificity. We also have done more investigation (in H. influenzae) into the details of the uptake specificity, measuring uptake with a series of uptake sequences altered at single or double positions. And Aim I of our proposal will give us an immensely detailed characterization of how strongly every base at every uptake sequence position contributes to uptake.
Another defense is that we have thought more deeply about how uptake could work than others have. Nobody else has considered that it's not enough to have a type four pilus or pseudopilus pull on the DNA (a ratchet is needed). Furthermore, nobody else has recognized the significance of the ability to take up circular molecules intact.
These issues are better addressed in H. influenzae. The need for a ratchet is not obvious in Neisseria, because it has long external pili. But most competent bacteria appear to pull DNA to the inner/cytoplasmic membrane with short stubby structures (pseudopili). Neisseria doesn't need long pili either, but this is only seen in mutants, whereas in H. influenzae we're studying the natural mechanism, not an aberration. We know that H. influenzae can take up circular DNAs that remain supercoiled in the periplasm, but we don't know that for Neisseria.
We will downplay testing whether competent H. influenzae have external pili. None are visible in the few published electron micrographs of competent cells, but nobody has ever specifically looked for them. We will begin with the reasonable assumption that competent cells lack external pili but will check this assumption using an anti-pilin antibody.
We may also downplay the search for the proteins that bind to DNA. It's intellectually messy work and we don't have any experience with mass-spec.
* The reviewers' emphasis on Neisseria made us wonder if one or both of them might have a Neisseria background. But I just checked the member lists for the previous two versions of this review committee, and none of them have any obvious connections to Neisseria or natural competence or pili. (These are previous committees, the membership list for our actual committee won't be released for months.) But whoever our reviewers were, they were surprisingly knowledgable!
If I'm on sabbatical why can't I get into the lab?
Well, the NIH proposal needs to get to Research Services in three weeks. I've received lots of very helpful advice, but it's mostly big-picture stuff that will take lots of work to implement. Lots of digging up papers (and reading them), lots of thinking about how stuff ties together, lots of trying to craft plausible descriptions of the significance for human health. Not to mention lots of struggling to understand what the post-doc is finding in all the wonderful sequencing data.
(I just realized that I should take advantage of the NIH database of funded proposals - I can search the list for 'recombination' + 'bacteria' to see the kinds of things people write. I also think I might focus the significance a bit more on H. influenzae, rather than just emphasizing the generality of the need to better understand recombination.)
The failed CIHR proposal also needs to be rewritten in the next few weeks, so we can get a draft to internal review a month before the due date. The research associate has offered to go through the reviewer's concerns, annotating the draft at each point that needs work. I'm afraid that this will be much of the proposal. She's working hard to get more preliminary data on our cross-species complementation plan. The concern is that her preliminary data could show that this isn't going to work as easily as we are hoping, so this is risky. Luckily the reviewers weren't concerned about the lack of preliminary data for the optical tweezers section - instead they were concerned about it's significance.
On Monday afternoon I'm giving a talk about DNA uptake to the biophysics group at the university across town (henceforth SFU) where I'll be doing my optical tweezers sabbatical project. This will be a chalk talk because I want to keep it informal and get lots of interaction with the audience, and because I don't want to take the time to prepare polished slides. Luckily the room's walls are covered with chalkboards, and the organizer has promised coloured chalk.
I'll prepare for this talk by rereading the CIHR proposal (killing two birds with one stone).
Bad news from CIHR
Yesterday I got the review and scores for our DNA uptake grant proposal - not nearly as good as I'd hoped. It only made the 51st percentile, which means it won't get funded.
The reviewers said some good things. They thought it was very well written (as it was). They liked the mix of risky and safe projects.
Some of the reviewers' concerns were very reasonable: the mass- spec bit lacked details that would make it credible (we've no experience); the basic cross-species complementation should have been tested; the search for a pilT homolog should have been completed; why continue to look for pili when they're not seen in EM. They also want more justification of the personnel budget. These problems can easily be addressed in the resubmission (due March 1).
Others mainly asked for better explanation of significance. Why study DNA uptake in H. influenzae when we already have information about uptake by Neisseria and Bacillus? What will we learn from the optical tweezers experiments? I thought we had done a really good job of explaining this, but I guess I thought wrong.
A bigger concern was the reviewers' general lack of enthusiasm, which I suspect may also account for several unfounded criticisms. One reviewer wondered why we were going to look at binding of Neisseria pili to DNA, when we had clearly stated that this was just a positive control. Another said that the optical tweezers experiments had already been done for Neisseria and Myxococcus, when in fact these had only looked at pilus retraction, not DNA uptake. If we had managed to create more enthusiasm, maybe the reviewers would have more carefully checked whether these criticisms were valid.
CIHR includes a 'community reviewer' for each proposal. These are interested members of the general public - they usually read only the lay summary. The community reviewer of the previous submission (3 years ago) complained that the lay summary hadn't included the name of the organism, so this time I made a point of naming Haemophilus influenzae, clearly explaining that it was a bacterium that causes respiratory diseases. But the reviewer of this proposal nevertheless complains that the name misled them into thinking this proposal was about influenza, and recommends that we don't give any species names!
We're going to try to get a revised version done by the end of January, so we can take advantage of UBC's internal review option.
The US-variation manuscript finally is coming together
(Yes, I know I've said this before...)
Abstract
Uptake signal sequences are DNA motifs that promote DNA uptake by competent bacteria in the family Pasteurellaceae and the genus Neisseria. The genomes of these bacteria contain many copies of their canonical uptake sequence (often >100-fold overrepresentation), causing the uptake machinery to prefer DNA derived from close relatives over DNAs from other sources. However the molecular and evolutionary forces responsible for both the uptake bias and the abundance of uptake sequences in these genomes are not well understood. Here we thoroughly evaluate the simplest explanation, that uptake sequences accumulate in genomes by a form of molecular drive, generated by biased DNA uptake and genetically neutral recombination. A computer simulation model shows that these simple assumptions are sufficient to drive uptake sequences to high densities, with the spacings, stabilities and strong consensuses typical of real uptake sequences. In the absence of strong evidence of selection for a recombination function, it may thus be more parsimonious to treat uptake sequences as an epiphenomenon of biased DNA uptake rather than as evidence for a sexual function of natural competence.
Abstract
Uptake signal sequences are DNA motifs that promote DNA uptake by competent bacteria in the family Pasteurellaceae and the genus Neisseria. The genomes of these bacteria contain many copies of their canonical uptake sequence (often >100-fold overrepresentation), causing the uptake machinery to prefer DNA derived from close relatives over DNAs from other sources. However the molecular and evolutionary forces responsible for both the uptake bias and the abundance of uptake sequences in these genomes are not well understood. Here we thoroughly evaluate the simplest explanation, that uptake sequences accumulate in genomes by a form of molecular drive, generated by biased DNA uptake and genetically neutral recombination. A computer simulation model shows that these simple assumptions are sufficient to drive uptake sequences to high densities, with the spacings, stabilities and strong consensuses typical of real uptake sequences. In the absence of strong evidence of selection for a recombination function, it may thus be more parsimonious to treat uptake sequences as an epiphenomenon of biased DNA uptake rather than as evidence for a sexual function of natural competence.
Resolving the hotspot paradox, at least partly)
A while back I described our previous work on the paradoxical activity of meiotic recombination hotspots (their mode of action is self-destructive). A new paper by Simon Myers and coauthors (Drive Against Hotspot Motifs in Primates Implicates the PRDM9 Gene in Meiotic Recombination.) now goes a long way towards resolving the paradox, though it doesn't explain how our recombination system got itself into this mess.
This group had previously identified a 13-nt sequence motif typical of human hotspots (thought not all of them); it's thought to be the sequence motif recognized by the process that initiates recombination by creating a double-strand break in the hotspot DNA. Previous work had suggested that chimpanzee hotspots are in different places than human hotspots, so the authors looked at the chimpanzee homologs of the human hotspots and found that although the sites did have this sequence (or variants of it), they didn't function as hotspots. The chimpanzee genome also had this motif at other sites, more than the human genome does. They concluded that many of the human occurrences of the motif had been lost from the human genome because their hotspot activity was self-destructive. They hypothesized that the motif was not ancestrally a hotspot but had become one in the human lineage, 1-2 million years ago.
They then decided to look for the protein that recognizes these sites. Based on their earlier work they had already hypothesized that it would be a zinc-finger protein with ≥12 'fingers' to bind the motif. So they used structural predictions to examine candidate zinc-finger proteins encoded by the human genome, and found five candidates, of which the best was a protein called PRDM9.
If PRDM9 is indeed the protein that, in humans, binds the 13 nt hotspot motif to initiate recombination, its human version should recognize this motif but its chimpanzee version should not. Consistent with this, PRDM9 was the only one of the five candidates that was different in chimpanzees (the other four had identical sequences in both species). Furthermore, it's sequence didn't just have random differences, but had many of its differences in the zinc-fingers that recognize DNA sequence,with hallmarks of positive selection for the changes. And independent work on this protein in mice and genetic mapping, both implicate it as playing a role in the initiation of recombination.
So what are the implications for the hotspot paradox? My simple view is that active hotspots do self-destruct over evolutionary time, as we predicted, and because we need recombination to hold chromosomes together in meiosis, this creates selection on the protein that recognizes them. Variant proteins that recognize new sequences are favoured (that's the positive selection) because they can cause more recombination and thus better prevent chromosome errors. So over long evolutionary periods, genomes may progress through a series of different hotspot motifs and locations.
Researchers have sometimes proposed that different kinds of genes evolve best with different amounts of recombination, and that the chromosomal locations of genes and/or hotspots have evolved to that optimize the amount of recombination. This new paper throws cold water on that idea.
Added later: Turns out the Myers paper was published together with two other papers about PRDM9's role in recombination, confirming and extending the conclusions. And, the same gene was identified last year as a locus very important in speciation, so maybe changing your hotspot specificity changes who you can reproduce with.
This group had previously identified a 13-nt sequence motif typical of human hotspots (thought not all of them); it's thought to be the sequence motif recognized by the process that initiates recombination by creating a double-strand break in the hotspot DNA. Previous work had suggested that chimpanzee hotspots are in different places than human hotspots, so the authors looked at the chimpanzee homologs of the human hotspots and found that although the sites did have this sequence (or variants of it), they didn't function as hotspots. The chimpanzee genome also had this motif at other sites, more than the human genome does. They concluded that many of the human occurrences of the motif had been lost from the human genome because their hotspot activity was self-destructive. They hypothesized that the motif was not ancestrally a hotspot but had become one in the human lineage, 1-2 million years ago.
They then decided to look for the protein that recognizes these sites. Based on their earlier work they had already hypothesized that it would be a zinc-finger protein with ≥12 'fingers' to bind the motif. So they used structural predictions to examine candidate zinc-finger proteins encoded by the human genome, and found five candidates, of which the best was a protein called PRDM9.
If PRDM9 is indeed the protein that, in humans, binds the 13 nt hotspot motif to initiate recombination, its human version should recognize this motif but its chimpanzee version should not. Consistent with this, PRDM9 was the only one of the five candidates that was different in chimpanzees (the other four had identical sequences in both species). Furthermore, it's sequence didn't just have random differences, but had many of its differences in the zinc-fingers that recognize DNA sequence,with hallmarks of positive selection for the changes. And independent work on this protein in mice and genetic mapping, both implicate it as playing a role in the initiation of recombination.
So what are the implications for the hotspot paradox? My simple view is that active hotspots do self-destruct over evolutionary time, as we predicted, and because we need recombination to hold chromosomes together in meiosis, this creates selection on the protein that recognizes them. Variant proteins that recognize new sequences are favoured (that's the positive selection) because they can cause more recombination and thus better prevent chromosome errors. So over long evolutionary periods, genomes may progress through a series of different hotspot motifs and locations.
Researchers have sometimes proposed that different kinds of genes evolve best with different amounts of recombination, and that the chromosomal locations of genes and/or hotspots have evolved to that optimize the amount of recombination. This new paper throws cold water on that idea.
Added later: Turns out the Myers paper was published together with two other papers about PRDM9's role in recombination, confirming and extending the conclusions. And, the same gene was identified last year as a locus very important in speciation, so maybe changing your hotspot specificity changes who you can reproduce with.
Two steps forward, one step back?
The work and ideas underlying the US variation manuscript are getting better, but the manuscript itself is getting farther from completion, not closer.
Advance #1: Realizing that I can use a log scale for the x-axis to see if runs have really reached equilibrium.
Retreat (the opposite of advance?) #1: Realizing that runs I had thought were at equilibrium aren't, so that conclusions I had thought were solid are not, so I don't really know what the true results are!
Advance #2: Realizing that I should think of/write about the elevated fragment mutation rates as degrees of divergence.
Advance #3: Remembered that the Introduction says that the goal of the work is to evaluate the drive hypothesis as a suitable null hypothesis for explaining uptake sequence evolution. Our results show that it is; the accumulation of uptake sequences under our model is strong, robust, and has properties resembling those of real uptake sequences.
Progress: Going through the Results section, annotating each paragraph with a summary of the all of the relevant data, annotated by whether this is solid equilibrium data (fit to use) or not. This is taking a lot of time, because I have to identify and check out (and sometimes enter and graph) the data, but the results aren't as bad as I had feared. Runs that have already finished fill some of the new-found gaps, and others are already running but won't finish for a few days (some longer). So I'm going to finish this annotation, queue whatever runs I think are still needed, and then maybe spend a few days on the optical tweezers prep work (at long last) while the runs finish.
Advance #1: Realizing that I can use a log scale for the x-axis to see if runs have really reached equilibrium.
Retreat (the opposite of advance?) #1: Realizing that runs I had thought were at equilibrium aren't, so that conclusions I had thought were solid are not, so I don't really know what the true results are!
Advance #2: Realizing that I should think of/write about the elevated fragment mutation rates as degrees of divergence.
Advance #3: Remembered that the Introduction says that the goal of the work is to evaluate the drive hypothesis as a suitable null hypothesis for explaining uptake sequence evolution. Our results show that it is; the accumulation of uptake sequences under our model is strong, robust, and has properties resembling those of real uptake sequences.
Progress: Going through the Results section, annotating each paragraph with a summary of the all of the relevant data, annotated by whether this is solid equilibrium data (fit to use) or not. This is taking a lot of time, because I have to identify and check out (and sometimes enter and graph) the data, but the results aren't as bad as I had feared. Runs that have already finished fill some of the new-found gaps, and others are already running but won't finish for a few days (some longer). So I'm going to finish this annotation, queue whatever runs I think are still needed, and then maybe spend a few days on the optical tweezers prep work (at long last) while the runs finish.
Two views of the same data
Here is some data from a series of runs where I simultaneously varied the lengths and numbers of the recombining fragments, so that the total amount of recombination remained the same (e.g. 1000 fragments 100 bp long or 50 fragments 2 kb long). I concluded that the runs were close to equilibrium and that the runs that got their recombination with the shortest fragments reached the highest equilibrium score.
But wait! This is the same data, now with the X-axis on a log scale. Now I see something quite different - after the first few cycles, the scores of all the runs are going up at the same rate (same slope), and their rate of increase is very log-linear. None of the runs show any sign of approaching equilibrium (i.e. of leveling off).I had said I would always do runs both from above (a seeded genome) and from below (a random-sequence genome) and take as equilibrium the score the up and down runs converged on. I didn't do that here, but I see I should have.
I don't know whether I've done any runs that went long enough that the score obviously leveled off when plotted on a log scale. If not I should.
***Later: Some of the runs I've done clearly do level off even on the log scale. This is good. But some of the runs that I've been treating as at equilibrium (runs for which I've done an up run but not a down run) haven't leveled off at all, so I'm not justified in making any assumptions about where they'll stop. Time to run them longer, and do some down run counterparts.
A clearer way to look at the mutation rates?
I think some of my problems understanding the effects of mutation rates in our model are created by the words I've been using, words that describe an aspect of what the model does rather than what it represents.
In most of the runs I've done, the genome being followed (the focal genome) mutates at a specified rate in each cycle (usually 0.0001 or 0.00001 mutations per bp), and the DNA fragments that are recombined mutate at a 100-fold higher rate. This is designed to simulate the fragments coming from cells that shared a common ancestor with the focal genome 50 generations ago. This is a biologically reasonable setup.
In the model itself the differences are handled as different mutation-rate settings that are applied to the same mutation-generating subroutine, and that's how I've been thinking of them. But I now think that referring to both types of changes (in the genome and in the fragment) as due to different mutation rates has created problems, causing me to feel that I have to justify using two different rates, and that the model would somehow be simpler or purer if the two rates were the same.
In the model itself the differences are handled as different mutation-rate settings that are applied to the same mutation-generating subroutine, and that's how I've been thinking of them. But I now think that referring to both types of changes (in the genome and in the fragment) as due to different mutation rates has created problems, causing me to feel that I have to justify using two different rates, and that the model would somehow be simpler or purer if the two rates were the same.
But what if I instead referred to changes in the fragments as being due to 100 generations of divergence, rather than to a 100-fold higher mutation rate? I'm going to try this and see if my thinking and writing become clearer.
Effects of mutations
One continuing puzzle about the results from the Perl simulation of uptake sequence variation is the independence of equilibrium score and mutation rate. It's true that mutations both create and destroy uptake sequences, but I wouldn't expect the effects to consistently cancel each other out. Even though that's what happened in a very simple mathematical model I did years ago.
I suspect that the interactions between mutation and uptake sequence accumulation are more subtle than their independence would seem to suggest. So here are several questions that I think I can quickly answer with more runs:
1. Does changing the proportionality of µg and µf change the equilibrium? (I already know there's about a 2-fold equilibrium score difference between 100:1 and 100:100, but I want to test more proportions.)
2. Does changing fragment length but keeping the number of fragments recombined per cycle the same change the equilibrium?
3. Does changing the fragment length but keeping the amount of DNA recombined the same change the equilibrium?
4. When µf = µg, does changing the fragment length but keeping the number of fragments recombined per cycle the same have no effect? Maybe not, because long fragments are more likely to change other US?
I suspect that the interactions between mutation and uptake sequence accumulation are more subtle than their independence would seem to suggest. So here are several questions that I think I can quickly answer with more runs:
1. Does changing the proportionality of µg and µf change the equilibrium? (I already know there's about a 2-fold equilibrium score difference between 100:1 and 100:100, but I want to test more proportions.)
2. Does changing fragment length but keeping the number of fragments recombined per cycle the same change the equilibrium?
3. Does changing the fragment length but keeping the amount of DNA recombined the same change the equilibrium?
4. When µf = µg, does changing the fragment length but keeping the number of fragments recombined per cycle the same have no effect? Maybe not, because long fragments are more likely to change other US?
Line breaks in Word 2008
I have to chop a 200 kb file into 20 kb pieces, because the USS position weight matrix I'm using (derived from Gibbs analysis of the H. influenzae genome) is so fastidious (???) that runs take forever. Specifically a 200 kb simulation that's using a pre-evolved sequence with quite a few uptake sequences already in it has taken 28 days to complete about 3300 cycles and it's about to exceed its pre-specified time limit (800 hours, about 33 days) and be terminated before it finishes. Terminating prematurely means that it won't report the sequence it has to painstakingly evolved. And I had even given it a tenfold higher mutation rate to help it run fast!
Anyway, my clumsy solution was to chop the 200 kb input sequence into ten 20 kb segments, and evolve them all in parallel. Because Word is good with work counts, I opened the sequence file (as a text file) in Word and marked off every 20 kb with a couple of line breaks. Then I opened the file in Textedit and deleted everything except the last 20 kb to get a test file (no line breaks at all, that I could see). But it generated an 'unrecognized base' error message when I tried to use it, so my first suspicion was that Word had somehow generated a non-Unix line break.
Sure enough, opening the file in Komodo showed that it had. But surprisingly, the problem wasn't a Mac-style line break, but a DOS/Windows line break! Maybe Word 2008 thinks all .txt files are for Windows?
Anyway, my clumsy solution was to chop the 200 kb input sequence into ten 20 kb segments, and evolve them all in parallel. Because Word is good with work counts, I opened the sequence file (as a text file) in Word and marked off every 20 kb with a couple of line breaks. Then I opened the file in Textedit and deleted everything except the last 20 kb to get a test file (no line breaks at all, that I could see). But it generated an 'unrecognized base' error message when I tried to use it, so my first suspicion was that Word had somehow generated a non-Unix line break.
Sure enough, opening the file in Komodo showed that it had. But surprisingly, the problem wasn't a Mac-style line break, but a DOS/Windows line break! Maybe Word 2008 thinks all .txt files are for Windows?
My coauthors cut the Gibbs analysis!
Well, not completely, they give it a single paragraph, but without any explanation of what the Gibbs motif sampler does or why that's important. I'm going to expand it back to a few paragraphs (maybe half of its original length). What will this say?
First, that we need to be using uptake sequence datasets that reflect how uptake sequences actually evolve (as motifs). We need information about both the nature of the motif for each genome (as a position weight matrix) and the positions of sequences fitting this motif. The matrix won't necessarily reflect the true biases of the respective uptake systems, but it's the best estimate we have.
Second, that Gibbs analysis found many more positions, but that the matrices based on these gave logos similar to those from previous searches for core-consensus and singly-mismatched uptake sequences. Not surprisingly these logos gave more weight to the flanking sequences that had been omitted from the core-consensus searches.
Third, that we did the Gibbs analysis for all genomes with uptake sequences.
Fourth, that we used the datasets to analyze patterns previously reported, and found no evidence of motif differences due to direction of replication or transcription, nor to location in translated vs untranslated regions.
Fifth, the more extensive variation in the Gibbs datasets allowed us to look for covariation between the bases present at different positions of DUS and USS. The only covariation this found was between very close positions, indicating that more distant interactions between bases are unlikely to play roles in uptake.
Time to think about doing an experiment!
OK, the draft NIH proposal is in the hands of the internal reviewers. Early in January they'll give me lots of (I hope harsh) feedback on what needs to be fixed. Till then, I've got two big things on my plate.
One is the US variation manuscript. It isn't exactly on my plate yet, as my coauthors are still assembling their drastic revisions back into a coherent manuscript, but they say I should get it tomorrow. I'm hoping it's now in pretty good shape, with my job now just to polish the writing and the figures so we can get it submitted within a few weeks.
The other is beginning the groundwork for the optical tweezers experiments. Let's see what I can remember about what needs to be done. In general, I'm going to use Bacillus subtilis cells as my positive control, because they're bigger and tougher than H. influenzae. They're also naturally competent, and were successfully used for an optical tweezers study of DNA uptake in 2004.
1. I need to be able to stick cells onto glass coverslips without killing them or otherwise preventing them from taking up DNA. I'll start with Bacillus subtilis, and with poly-L-lysine coated cover slips. I'll need to make these myself - I have several protocols and several offers of help, but don't know if any of these people will be around over the holidays. The alternative to poly-L-lysine is a silane solution (fancy name) that was used for the B. subtilis experiments. But I don't have a protocol for using this, so it's a bit of a crapshoot. Some of the poly-L-lysine protocols say to pre-clean the coverslips with strong acid (nitric? chromic?) - a researcher down the hall said he might have some (old-tyme labs are good to have around).
2. I need to attach streptavidin to polystyrene beads. I have a protocol, and the streptavidin, and the coupling reagent, and the ready-for-coupling beads (they may be a bit small, 1 µ rather than 2 µ, but they'll do). What I don't have is a good way to test how well the coupling has worked (see below).
3. I need some biotin-conjugated DNA (H. influenzae chromosomal DNA). The research associate made some a while back for a different experiment, but I don't know if there's any left, or where it would be. I could make my own, if I can find the biotin.
4. I need to make the B. subtilis competent. This means that I need to make up the appropriate culture medium and competence-inducing medium (2 kinds, as I recall), and the appropriate agar plates for selecting transformants (so I can test whether they really are competent).
5. Once I have the streptavidin-coated beads and the biotin-coupled DNA, and some competent cells, I can test whether cells will stick to beads that have been incubated with DNA but not to beads without DNA or to DNase-treated beads. If this works I will know that there's streptavidin on the beads and biotin on the DNA and the cells are competent. If it doesn't I'll only know that at least one thing isn't right.
6. At this stage I can also test whether the cells I've stuck onto a coverslip can still bind DNA, by giving them the beads-plus-DNA and seeing if the beads stick to the cells (with the same controls as in step 4). Oh, but first I have to make sure that the competent cells will also stick to the coverslips.
7. Then I can make some competent H. influenzae and try steps 5 and 6 with them. Assuming I've been able to stick the H. influenzae cells onto coverslips).
8. After all this is working, I'll be ready to go back to the physics lab and try to measure some forces!
One is the US variation manuscript. It isn't exactly on my plate yet, as my coauthors are still assembling their drastic revisions back into a coherent manuscript, but they say I should get it tomorrow. I'm hoping it's now in pretty good shape, with my job now just to polish the writing and the figures so we can get it submitted within a few weeks.
The other is beginning the groundwork for the optical tweezers experiments. Let's see what I can remember about what needs to be done. In general, I'm going to use Bacillus subtilis cells as my positive control, because they're bigger and tougher than H. influenzae. They're also naturally competent, and were successfully used for an optical tweezers study of DNA uptake in 2004.
1. I need to be able to stick cells onto glass coverslips without killing them or otherwise preventing them from taking up DNA. I'll start with Bacillus subtilis, and with poly-L-lysine coated cover slips. I'll need to make these myself - I have several protocols and several offers of help, but don't know if any of these people will be around over the holidays. The alternative to poly-L-lysine is a silane solution (fancy name) that was used for the B. subtilis experiments. But I don't have a protocol for using this, so it's a bit of a crapshoot. Some of the poly-L-lysine protocols say to pre-clean the coverslips with strong acid (nitric? chromic?) - a researcher down the hall said he might have some (old-tyme labs are good to have around).
2. I need to attach streptavidin to polystyrene beads. I have a protocol, and the streptavidin, and the coupling reagent, and the ready-for-coupling beads (they may be a bit small, 1 µ rather than 2 µ, but they'll do). What I don't have is a good way to test how well the coupling has worked (see below).
3. I need some biotin-conjugated DNA (H. influenzae chromosomal DNA). The research associate made some a while back for a different experiment, but I don't know if there's any left, or where it would be. I could make my own, if I can find the biotin.
4. I need to make the B. subtilis competent. This means that I need to make up the appropriate culture medium and competence-inducing medium (2 kinds, as I recall), and the appropriate agar plates for selecting transformants (so I can test whether they really are competent).
5. Once I have the streptavidin-coated beads and the biotin-coupled DNA, and some competent cells, I can test whether cells will stick to beads that have been incubated with DNA but not to beads without DNA or to DNase-treated beads. If this works I will know that there's streptavidin on the beads and biotin on the DNA and the cells are competent. If it doesn't I'll only know that at least one thing isn't right.
6. At this stage I can also test whether the cells I've stuck onto a coverslip can still bind DNA, by giving them the beads-plus-DNA and seeing if the beads stick to the cells (with the same controls as in step 4). Oh, but first I have to make sure that the competent cells will also stick to the coverslips.
7. Then I can make some competent H. influenzae and try steps 5 and 6 with them. Assuming I've been able to stick the H. influenzae cells onto coverslips).
8. After all this is working, I'll be ready to go back to the physics lab and try to measure some forces!
A draft NIH proposal
With the US variation manuscript in the hands of my co-authors, I've spent the past week working on our planned proposal to NIH. It's not due till the beginning of February, but I have some internal reviewers lined up and I promised I'd get them a presentable draft by today. Which I will - this morning I just have to tidy up the last bit (how we'll characterize the transformability QTLs we hope to find) and polish a couple of paragraphs. (Note that this is far in advance of my usual grant-writing schedule - feels good).
We have three Specific Aims: 1. Characterize recombination tracts in individual transformants. 2. Measure recombination efficiencies across the genome, in pooled transformant genomes. 3. Identify loci responsible for transformability differences.
There's still lots of work to be done once I hear back from the reviewers (hopefully in a couple of weeks). The Methods aren't yet as good as they can be (assuming the goals don't change, which they might). The preliminary sequence data needs more analyzing and there are a couple of preliminary experiments we really need to do. The 'grantsmanship' needs LOTS of work (more selling of us, more potential problems and fallbacks). There aren't any references yet. The writing still needs work, but not until after the content is improved.
And I've done nothing about the other parts of the proposal (Budget etc).
In the meantime, my co-authors have sent me their revised draft of the US variation manuscript...
Manuscript progress
The US variation manuscript is in the hands of my co-authors. They've taken a step that I thought might be needed but I had lacked the stamina to undertake - rearranging everything so it starts with the analysis of multiplicatively scored simulations rather than additively scored ones.
I didn't want to do this only because it would mean setting up and analyzing yet more simulation runs. That's because there were some variables for which I had good data for the additive case (which I was presenting), but less thoroughly done data for the multiplicative case. It's not that I had any reason to doubt that the multiplicative data I had was correct - it just wasn't sufficiently replicated to make good figures.
Luckily, now that my co-authors have dealt with the reorganization, there turn out to be only a few cases needing more work. I think most of these runs are now done, but I still have to analyze the results and generate figures.
But I've promised to have a semi-presentable version of our NIH proposal ready for the internal reviewers by Monday, so the US variation data analysis will have to wait until that's done.
We have a plan (again, but it's a new plan)
Specific Aims, in the form of questions:
Aim I. Characterizing the genetic consequences of transformation:
Aim I. Characterizing the genetic consequences of transformation:
A. How do transformant genomes differ from the recipient genome? We want to know the number and length distributions of recombination tracts. This will be answered by sequencing a number of recombinant genomes (20? more?), preferably using multiplexing. We have preliminary data (analysis of four) showing 3% recombination.Aim 2. Characterizing the genetic differences that cause strain-to-strain variation in transformability: (The results of Part A will guide design of these experiments.)
B. How much do recombination frequencies vary across the genome? This will be measured by sequencing a large pool of recombinant genomes. The sensitivity of this analysis will be compromised by various factors - some we can control, some we can't.
C. Are these properties consistent across different strains? We should do 2 or more transformants of 86-028NP and of a couple of other transformable strains.
D. How mutagenic is transformation for recombined sequences? For non-recombined sequences? Is mutagenicity eliminated in a mismatch repair mutant? If not, is it due to events during uptake or translocation?
A. What loci cause strain 86-028NP to be ~1000-fold less transformable than strain Rd? (Are any of these loci not in the CRP-S regulon?) We will identify these by sequencing Rd recombinants (individually and/or in one or more pools) pre-selected for reduced transformability.In the Approach section we'll explain how we will accomplish these aims, and why we have chosen these methods. In the Significance and Innovation sections we'll need to convince the reader that these aims will make a big difference to our understanding of bacterial variation and evolution.
B. What is the effect of each 86-028NP allele on transformability of Rd, and of the corresponding Rd allele on 86-028NP? Are the effects additive? Do some affect uptake and others affect recombination?
C. Are transformation differences in other strains due to the same or different loci? This can be a repeat of the analysis done in Aim 2A. Does each strain have a single primary defect?
D. How have these alleles evolved? Have they been transferred from other strains? Do defective alleles have multiple mutations, suggesting they are old?
Aim 1 will provide fundamental information about bacterial recombination (and associated mutation), which will put almost all studies of bacterial evolution on a more solid footing. Aim 2 will help us understand why natural transformation has such dramatic variation in populations of many different bacteria, and thus how natural selection and other processes act on transformability.
Bacillus subtilis
Yesterday I streaked out some old B. subtilis strains that I would like to use as positive controls for the optical-tweezers experiments.You gotta love bacteria that are still fully viable after 18 years as a slant in the refrigerator (not the freezer, the fridge).
My turn to do lab meeting, yet again!
(I really do need to get some more people into the lab.)
What will I talk about? I wish I'd been doing some experiments. What did I talk about last time? I don't have my notes here, but I think it was the US variation manuscript - I think I went through the figures. Since then I've mostly been working on the NIH proposal, so I guess that's the best thing to talk about.
The Specific Aims keep morphing. Here's what I thought was the stable version:
Aim 1. Characterize the recombinome by sequencing DNA from millions of pooled transformants.
Aim 2. Characterize the biases of the steps that make up the recombinome, by sequencing:
a) millions of chromosomal DNA fragments and degenerate uptake sequences taken up by competent cells,
b) chromosomal DNA fragments taken into the the cytoplasm of competent cells,
c) chromosomal DNA recombined by a non-RecA recombinase,
d) DNA of millions of transformants of a strain unable to do mismatch repair.Aim 3. Map loci responsible for transformation differences between two strains.
But the post-doc's new data suggests high mutation rates in recombined sequences, and this may mean that we should put more emphasis on what he calls the transmission genetics. That is, we should first pin down the general properties of what actually gets recombined. How much DNA is typically replaced? In how many segments? What is their size distribution? Are tracts of donor DNA interrupted by recipient alleles? Do indels recombine cleanly, by homologous recombination in flanking sequences, or do we see non-homologous recombination at one end? What is the frequency of new mutations in recombined DNA (and in the rest of the genome)? This information is best obtained by sequencing the DNA of individual transformants, not a big pool.
This should probably become (part of?) our first Aim. Should it be an Aim in itself? Will we then have too many Aims?
I can see two different directions we could take this: I. We could make a big shift in direction, getting rid of all of Aim 2 and expanding Aim 3 to include more strains. That would give a much more streamlined proposal, one focused on the consequences of recombination and not the component steps. Or II. we could get rid of Aim 3, keeping the focus on the processes that give rise to recombinant genomes. Both are areas I think are really important. Direction I fits well with the work a previous post-doc did, characterizing the variation in DNA uptake and transformability of a wide range of H. influenzae strains. Direction II fits better with my desire to understand the role of uptake sequences, but this goal is really only addressed by Aim 2 a, and that's already included in another proposal, the one we submitted to CIHR in September.
In either case we should probably demote Aim 2 c to an optional goal, unless we can get the data showing that this alternate recombinase (lambda Red) does indeed work in H. influenzae. That would be a very cool result, but it's not central to this proposal.
Subscribe to:
Posts (Atom)