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in The Biology Files
So for the next two weeks I'll only have to think about the CIHR proposal. It's due Sept. 15, but I'll need to click the submit button Sept. 13 (Sunday), because I'll be traveling on the 14th and 15th. (The paperwork (electronic and real) needs to be in a few days before that.)
Although the reviewers thought that the previous version of the proposal was well written, I now see that the overall structure was weak. In particular, the Introduction (a short section, only 3 paragraphs) introduced competence but failed to introduce the problem/s I want to address, the hypothesis/hypotheses I was testing, or the approach I will take to test the hypothesis/hypotheses. That was because I hadn't done a good enough job of spelling these out even to myself. So here's a new attempt:
The phenomenon: Bacteria actively transport DNA molecules into their cells, across their outer and inner membranes.
The specific problems this proposal addresses: How does H. influenzae transport DNA across its outer membrane: (a) How is this uptake initiated? (b) How are long fragments pulled into the periplasm? (c) Why is uptake so strongly biased towards specific sequences?
The hypotheses: (1) Initiation and progression of DNA uptake are mechanistically distinct processes. (2) Uptake sequences are favoured because they facilitate the DNA deformation needed to initiate uptake. (3) Progression of uptake uses an ATP-driven ratchet driven by assembly and disassembly of type four pseudopili (this hypothesis may well be wrong, but that's OK).
The Specific Aims: (1) We will fully characterize the uptake specificity, using both synthetic sequences and the full H. influenzae genome. (2) We will identify the proteins that contact DNA during uptake and those responsible for the sequence specificity. (3) We will test whether the uptake sequence motif polarizes uptake and whether it promotes DNA kinking. (4) We will characterize the forces acting on DNA during binding and uptake.
I'm going to paste this summary on the first page of my draft proposal, so I incorporate it into the Introduction and use the Background to establish the problems and build to the hypotheses.
To get evidence for USS-dependent binding, we should collect data for a histogram of rupture forces (i.e. how strong a pull is needed to break the bead free of the cell), for DNAs with and without USS. If binding is distinct from uptake, this distribution should be bimodal, probably with a much higher peak for the low 'binding' rupture force. She said this would be quite a lot of work (weeks, at least).
Can we stick H. influenzae cells onto a glass coverslip, (as the B. subtilis people did) rather than restraining them with a micropipette? This would make the manipulations much easier. She recommended trying BSA-coated coverslips as well as silane-coated ones. The coating will also help reduce non-specific sticking of DNA to the glass.
To test whether uptake is due to 'diffusive motor' or a 'power stroke' (I'll need to read up on these concepts) we should create a force-velocity curve. If we find that, below a critical stalling point, the velocity of DNA uptake is independent of the opposing force pulling the bead back into the center of the laser trap, we would conclude that uptake was due to machinery exerting a power stroke, whereas if we observed a gradual slowing of uptake with increasing opposing force, it would be due to a diffusive motor. I think Tfp use a power stroke, and a process driven by flow of ions (maybe the PMF (= proton motive force?) would be diffusive. The B. subtilis rate is largely independent of the opposing force on the bead, although it appears to somehow be generated by the PMF.
If uptake is indeed mediated by a short pseudopilus that acts as a ratchet on the DNA, we might be able to see the ratcheting in a velocity vs time (or force vs time?) graph. This would depend on the resolution of the velocity (or force?) measurements. If the pseudopilus is only, say 20 nm long (a guess of the thickness of the periplasm), we would need to detect fluctuations on this scale.
In principle optical traps can exert forces greater than 100 pN on trapped beads. However DNA deforms at 65 pN, allowing it to stretch. Not only will such stretching complicate length/velocity measurements but the deformation may perturb interactions with the uptake proteins, causing them to lose their grip on the DNA. So we should keep our measurements below about 60 pN.
She recommended making a flow chart to lay out the tests we will do and how the results will affect our hypotheses and guide our next steps.
IN HIS NEWS FOCUS STORY “ON THE ORIGIN of sexual reproduction” (5 June, p. 1254), C. Zimmer highlights the importance of the phylogenetic perspective championed by John Logsdon, but by considering only eukaryotes he overlooks an important bacterial clue to the evolution-of-sex puzzle.
Until recently, bacteria were thought to be sexual; they have well-characterized processes that cause recombination of chromosomal alleles, and these parasexual processes were assumed to have evolved for recombination in the same way as meiotic sex in eukaryotes. However, a more critical analysis of the genes responsible for the parasexual processes suggests that they did not evolve for sex after all. Instead, the chromosomal recombination they cause appears to arise as unselected effects of related processes, the evolutionary functions of which are well established (1).
The fact that bacteria lack genes evolved for recombination indicates that meiotic sex must have evolved in eukaryotes to solve a problem that bacteria don’t have. Bacteria apparently get whatever recombination they need by accident—why do eukaryotes need so much more?
ROSEMARY J. REDFIELD
Department of Zoology, University of British Columbia, Vancouver, BC V6T 3Z4, Canada. E-mail: firstname.lastname@example.org
I can come up with a hypothesis for the first parts (the ones covered by the current post-doc's NIH fellowship proposal). "Every stage of transformational recombination is limited by sequence biases." This hypothesis might well be false - we only know of biases at two steps: DNA uptake and mismatch repair. But it provides a clear explicit framework for finding out where and what the biases are.
But I would like to extend the research to include the biases due to the differences in different isolates. Well, that's a way of saying it that sort-of fits the hypothesis but doesn't really capture what I want to propose. Instead I should first describe what I would like to propose, and then try to find a way to describe it that can be part of a unified hypothesis.
I would like to propose to find out the molecular reasons why different isolates of H. influenzae differ so much in their ability to transform. This should be fairly straightforward, given the molecular and genetic/genomic tools we have. We can also try to estimate how long these strains have had their specific transformation phenotypes - did a very recent ancestor get a mutation (or recombination!) that inactivated a competence/transformation gene, or is it descended from a long lineage of non-competent ancestors.
But I would also like to find out how different are the recombination histories of strains that can and can't transform - looking not just at the individual sequences they have acquired, replaced, or lost, but at the pattern underlying these events. Do strains that don't transform at all in the lab have a history of greatly reduced recombination, relative to strains that transform very well in the lab?
I don't know how do-able this is. If we get genome sequences of enough strains, can we build up a detailed picture of their recombination histories? The previous post-doc used a program called Mauve to identify recombination tracts...
I also don't know to what extent this analysis will be facilitated by the information we'll get from the first parts described above. We'll first build up a complete picture of the relationship between (i) a pair of donor and recipient genomes and (ii) the recombinant genomes that result from DNA uptake. (If resources permit we can do more than one pair of genomes.) Then we try to use this knowledge to infer the recombinational histories of other genomes. Is there a hypothesis in there? Maybe the hypothesis is that this will be possible. We could hypothesize that "Understanding the limits to transformational recombination in lab cultures will let us identify the recombination histories of natural isolates."
But as science this is what I consider a 'pseudo-hypothesis'. It's not a hypothesis about the nature of reality, but a hypothesis about the nature of our abilities. How about "The limits to transformational recombination in lab cultures explain the recombination histories of natural isolates."
Hmm, if that's our hypothesis then maybe this proposal does belong in the Evolution of Infections Disease program after all, and not in the Prokaryotic Cell Growth, Differentiation and Adaptation program. I think I'll handle this question by putting together a decent summary (once we have a single hypothesis) and asking both Program Directors where they think it belongs.
A potential postdoc is interested in the role of gene exchange in natural populations, and I think this might be a very nice way to build on other work we've done and will be doing. It would also fit well into the NIH proposal we're preparing.
Work we've done: We know that DNA uptake and transformability are very variable in natural populations, but we don't know why (neither the molecular nor the evolutionary/ecological 'why'). The best study was by a recent postdoc, who analyzed 30+ natural isolates of H. influenzae for both DNA uptake and transformation. She found that very few took up as much DNA or transformed as well as the lab strain KW20. Some of these strains had sequenced genomes, but in most cases the genotype did not explain the phenotype.
Work we will be doing: A new postdoc is investigating the molecular constraints on transformation, to fully characterize the sequence biases that affect each stage of DNA uptake and recombination. This should give us a good picture of what transformational recombination looks like, at the genome-wide level.
The nice extension has two parts:
Part 1: Before we can hope to understand the evolutionary cause of the variation in competence and transformability, we need to find out its molecular causes - what are the genetic changes underlying the differences in DNA uptake and transformation? This is probably best done by a combination of genetics and genome sequencing. Genome sequencing has gotten so cheap that we can afford to do a lot of strains, not probably to the assembly stage (too much person-work), but enough to get the sequences of all the homologs of genes known from KW20 and other strains with assembled genomes. We could certainly do all the strains the postdoc characterized, but we might be able to do a much more comprehensive survey. (Maybe someone else is already doing this... I've just emailed the likely suspect so we can coordinate our efforts.)
With lots of genome sequences of strains of known phenotype, we can look for the individual causes of the different competence phenotypes and also look for patterns in these causes. Identifying the causes for individual strains will entail benchwork, using natural transformation to confirm that specific alleles are responsible for specific phenotypes. I would think that some of this could be a project for an undergraduate or M.Sc. student, but the new post-doc is bursting with ideas of how to do this efficiently for many strains - I’ll let him post these on his blog. Then we can ask whether the causes appear to be a random subset of the possible mutations, or whether there are consistent causes in the different strains. We can also ask how recent the changes are (have multiple mutations accumulated in the competence genes?), and maybe even ask whether the most recent ancestors were indeed competent (but this may not be possible - see our recent PLoS One paper).
Part 2: Once we have genome sequences and the results of the other post-doc’s genome-wide recombination analysis, we can not only examine the genomes for evidence of recombination, but also ask whether the recombination fits the pattern expected for transformation, and whether the differences in recombination correlate in any way with the differences in transformability. For example, do nontransformable strains have a history of reduced recombination? If yes, can we tell how recent this is? And is only the transformational component of recombination reduced? Is there evidence that transformation by other causes (conjugation, transduction) is increased in strains that don't transform? Can we tell whether the changes causing reduced competence and transformability are themselves due to recombination?
This is a great project because it can go in lots of directions and because all of the possible answers are interesting.
Years ago I had a grad student working on a related question, and part of our motivation was the issue of whether sequence specificity is intrinsic to the process of DNA uptake, as is predicted by our hypothesis that it's a way to help get stiff inflexible DNAs across the outer membrane. If instead the specificity is caused by a protein external to the uptake machinery, this would be consistent with hypotheses positing a benefit of screening DNA for relatedness before letting it into the cell.
The practical obstacle to answering this question is that we have no good assay for DNA binding (and of course also no mutants that can still bind DNA but can't take it up). At present, DNA binding must be measured indirectly, by giving cells radioactively labeled DNA and comparing cell-associated cpm with and without pretreatment with DNase, which removes DNA that has bound to cells but not been taken inside them.
The Neisseria paper (Aas et al, 2002) took advantage of the pilT gene, which H. influenzae and its relatives don't have. They showed that wildtype Neisseria cells associate with DNA, and that this does not require the DUS uptake sequence. Wildtype cells take up most of the DUS-containing DNA they bind - after a 30 minute incubation about 70% of the cell-associated DNA is DNase I-resistant - but take up less than 1% of DNA lacking a DUS.
PilT retracts the type 4 pili filaments thought to bind DNA into the cell (mutants that don't make pili don't associate with DNA), and they predicted that cells lacking PilT would bind DNA to their surface but be unable to bring it in. But very little DNA associated with their pilT mutants even when no DNase I was used. So the non-specific DNA binding seen on wildtype cells requires not just the machinery thought to assemble pili but also the protein thought to disassemble them.
Cells lacking the major pilus protein (pilin) encoded by pilE don't have visible pili and they didn't bind DNA or take up DNA, but cells lacking the minor pilin-like protein encoded by comP do have visible pili and they bound DNA normally, but they didn't take any of it up even if it had DUSs. Overexpressing the normally-scarce ComP protein increased by 20-fold the amount of DNA bound and taken up, and proportionately increased the transformation frequency. This increased uptake was specific for DNA containing a DUS, although a modest increase was also seen for DNA that lacked DUS.
Overexpressing ComP also caused increased and DUS-dependent DNA uptake by cells carrying a knockout of pilT, although the effect was small - these cells took up only about 5% as much DNA as wildtype cells with normal ComP expression.
What does all this mean? Because they couldn't show that ComP binds DNA, the authors concluded that it probably acts indirectly, by activating or stabilizing another component that does the DNA binding. They also thought that ComP may normally act as a minor component of pili composed mainly of PilE. They also suggested that pilus retraction by PilT may not be the main force pulling DNA into the cell; instead the DNA may be quickly handed over to a periplasmic receptor that does the bulk of the pulling-in.
The first goal is to get my mind clearly focused on them, so I'm starting by going through the draft proposal to CIHR, which at present is largely unchanged from its 2007 version. One (depressing) advance is that I now realize that the Introduction is a failure. It consists of three very nice paragraphs, clear and well-written. These paragraphs contain the following: 1) an introduction to natural competence; 2) the broad goals of my research program; 3) the medical relevance of DNA uptake and transformation. Unfortunately they're not the paragraphs the Introduction needs - most of the information they provide doesn't belong in the Introduction.
What should the Introduction introduce? The proposal is about the mechanism of DNA uptake, so it should probably start by framing the problem - that bacteria take up DNA but we don't know how the DNA gets across the membranes (maybe say why I think this is likely to be difficult). Maybe contrast this with uptake of simple molecules? And the medical relevance could be supplemented with some cell biology relevance - for understanding related processes, maybe getting a better picture of the roles and mechanism of type 4 pili. I should also reframe the broad goals of our research, with less emphasis on evolutionary function and more on the totality of competence.
I'm also reconsidering which committee I should direct this proposal to. The previous version went to the Microbiology and Infectious Diseases committee, partly because they had approved our previous proposal, but also because I was simultaneously sending a different proposal (on gene regulation) to the Biochemistry and Molecular Biology committee. That proposal was funded. This new proposal is quite biochemical, so I'm wondering if it should go the the BMB committee.
OK, now I need to reread the proposal, to once again remind myself of what it's all about.