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.

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.

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.

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.

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?

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?

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!

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:

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.

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?

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.)

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.

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?

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.

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.

Keyboard rehab

I wondered if the death of my Apple aluminum keyboard might be not a direct consequence of the tea I spilled in it, but rather due to starchy goo created when the tea contacted the millions of nanoparticle-sized cracker crumbs that had probably slipped through the narrow gaps surrounding the keys over the last two years.

So I again took the batteries out, and washed it for a long time under warm running water, massaging the keys to loosen any crud stuck under them. Then I dried it over night in the 37°C incubator (the one with a fan that circulates warm dry air).

And voila - it works fine again!

Grant writing

I'm beginning to think that years (decades) of espousing unpopular ideas have left me with an arrogance deficit.

Bacteria moving on surfaces

A colleague just sent me a manuscript about differences between bacterial cells growing in broth (or in soft agar) and the same cells growing on agar plates under conditions where they can use flagella to move across the agar surface. This is important work. When we study cell physiology we usually use cells that are growing in well mixed broth, because this lets us assume that all the cells are experiencing the same conditions (stochastic molecular-level factors excepted).

An aside: For similar reasons we usually use broth cultures in exponential growth, because we expect the physiology of such cells to be independent of the culture density. Once the density gets high enough to affect cell growth, the culture will no longer be growing exponentially, and minor differences in cell density can cause big differences in cell physiology. Unfortunately many microbiologists are very cavalier in their interpretation of 'exponential', and consider any culture whose growth hasn't obviously slowed as still being in log phase.

The usual lab alternative is to grow then on the surfaces of medium solidified with agar. This is quite convenient, as most kinds of bacteria can't move across the usual 1.5% agar, so isolated cells grow into colonies. The density of cells on an agar surface can get very high (a stiff paste of bacteria), because the cells are being fed from below by nutrients diffusing up through the agar.

Depending on the agar concentration, the film of liquid on the surface of the agar may be thick enough (?) to allow bacteria that have flagella to swim along the surface. Because the bacteria often move side-by-side in large groups this behaviour is called 'swarming'. Often swarming on agar surfaces is facilitated by surfactants that the bacteria produce, which reduce the surface tension of the aqueous layer. I've always assumed that bacteria living in soil and on other surfaces produce such surfactants as a way of getting surface-adsorbed nutrients into solution (that's how the surfactants we use in soaps and detergents do their job), but maybe surfactants are also advantageous for moving across surfaces with air-water interfaces, such as damp soil. The side-by-side cell orientation and movement may also be a consequence of surface-tension effects, as illustrated in this sketch.









One commonly observed effect of high density growth on agar is less sensitivity to antibiotics. We and many others have noticed that we need higher antibiotic concentrations on agar plates than in broth cultures (or vice versa, that antibiotic-resistant bacteria die if we grow them in broth at the same antibiotic concentration we used on agar plates). We also directly see density effects in our transformation assays - if we put a high density of antibiotic sensitive cells on a plate, we often see more 'background' growth of the sensitive cells. (Sometimes we see the opposite - resistant cells can't form colonies when they're surrounded by too many dying sensitive cells.)

But why would more dense bacteria be more resistant to an antibiotic? One possibility is that the individual cells aren't more resistant, but because more cells are present, more cells get lucky. If this were true we'd expect the number of cells in the 'background' to be directly proportional to the number of cells plated. A more common interpretation is that the presence of other cells somehow protects cells from the antibiotic. We know that resistant cells can protect sensitive cells from some antibiotics, if the mode of resistance is inactivation of the antibiotic. This is especially powerful if the resistant bacteria secrete an enzyme that inactivates the antibiotic, as is the case with ampicillin. This effect occurs both in broth and on agar plates.

But can sensitive cells protect other sensitive cells? Might dying cells somehow sop up antibiotic, reducing the concentration their neighbours are exposed to? Might an underlying layer of sensitive cells protect the cells above them from antibiotic?







The big problem I see is that bacteria are so small that concentrations will very rapidly equilibrate across them by diffusion. The agar in the plate is about 500 µ thick, and the cells are only about 1 µ thick, so there should be far more antibiotic molecules in the medium than the sensitive cells can bind**. Thus I don't see how a layer of sensitive bacteria could use up enough of the antibiotic to significantly reduce the effective concentration for the cells above. Even if the cell membrane is a barrier to diffusion of the antibiotic, there's going to be enough fluid around the cells for the antibiotic to diffuse through.

** But I haven't done the math. OK, back of the envelope calculation puts the number of molecules of antibiotic at about 10^15/ml (assume a m.w. of 5 x 10^2 and a concentration of 5 µg/ml). The density of cells on top of the agar might be 10^12/ml. If each cell were to bind 1000 molecules of antibiotic (that seems a lot, but maybe it's not), they would together bind up all the antibiotic from an agar layer equivalent to the thickness of the cell layer. But the thickness of even a very thick layer of cells is no more than a few % of the thickness of the agar, so the overall antibiotic concentration would only decrease by a few %.

eyboard kaput

or the first time in about 25 years of computer use, 've spilled some liquid tea with milk and sugar into my keyboard. t's one of those lovely tiny apple aluminum wirelss keyboards. t wasn't very much tea, and quickly took out the batteries and rinsed the keyboard very thoroughly with distilled water and dried it overnight in the 378 incubator. ut it's toast. haracters type while holding the shift key down don't appear, and the 's' and 'f' keys tend to get stuck on strings of 'sssss' and 'fffff' showing up randomly. hat's not happening right now, but you can see the effects of the shift problem.

uckily ondon rugs has new ones on sale for 69, so 'll try to get one tonight.

Choosing a topic for a NIH proposal

I'm reading some excellent grantwriting advice from the Nov. 12 issue of the NIH NIAD newsletter. It frames its suggestions with the instructions given to NIH reviewers, emphasizing that the most important thing they're looking for is evidence that the proposed research will have a significant impact on the field:

"Your ultimate task is to judge the likelihood that the proposed research will have an impact on advancing our understanding of the nature and behavior of living systems and the application of that knowledge to extend healthy life and reduce the burdens of illness and disability. Thus, the first assessment should be “Is it worthwhile to carry out the proposed study?”"

This is excellent advice, and I'm going through the draft we have now, identifying places where we can point to impacts in various fields (pathogenesis, recombination, evolution).

But I have a harder time relating to another part of the advice, on how to choose a topic to propose research on. It appears to be directed at people who know they want to get a research grant but don't really care what topic they'll be researching. "I know how to do A, B and C, so I'll propose to find out D."

PHS 398 gestalt

I've been trying to reorganize my initial NIH proposal outline, so it fits the new guidelines. Here's how I think I should be using the new format:

1. Use the 'Significance' section to build the reader's interest in the problem(s) our Specific Aims address.
2. Use the 'Innovation' section to build the reader's interest in the methods we will use to achieve our aims.
3. Use the 'Approach' section to convince the reader that we can accomplish our Aims.
4. Use the initial 'Specific Aims' page to summarize all of the above, both as an introduction for the few readers who will read the rest of the proposal and as a stand-alone summary for everyone else.

How should I divide up the 12 pages? 'Specific Aims' is limited to one page (not counted in the 12). 'Significance' can be several pages. It must provide all the background that motivates the work, but I guess it doesn't need to contain any background that's only needed for understanding the methods we'll use, as that can go in 'Approach'. The length of 'Innovation' depends on how much of our approach we need to describe in order to showcase its innovativeness. It can describe as innovative methods that are explained in detail later — it doesn't need to provide the convincing evidence of their innovativeness. A page will probably be plenty. That leaves about 8 pages for the Approach, where we describe everything we're going to do, with all the detailed hows and whys.

A paradigm shift for how I organize grant proposals?

Yesterday I put together a paragraph-by-paragraph outline for our NIH proposal, using the usual sensible order: One-page Summary, Introduction and Background, Specific Aims, Preliminary Results, Research Methods. Today NIH released the new official Instructions (new because they're reduced the page limit from 25 to 12, and streamlined the content). Here's the organization they want; I'm going to have to do a lot of rethinking to figure out where I should put the information I would normally present, what I should leave out, and what new issues I need to emphasize. Luckily I'm not the only person dealing with this change - everyone applying for the usual NIH RO1 grants has to now use this format:

Specific Aims

This comes first; it has a one-page limit. I think it must also serve as a Summary page, because I can't find any mention of a separate Summary in the Instructions.

• State concisely the goals of the proposed research and summarize the expected outcome(s), including the impact that the results of the proposed research will exert on the research field(s) involved.
• List succinctly the specific objectives of the research proposed, e.g., to test a stated hypothesis, create a novel design, solve a specific problem, challenge an existing paradigm or clinical practice, address a critical barrier to progress in the field, or develop new technology.

I don't think this will cause us much problem; it's sort-of what I usually try to do in the Summary page anyway.

(a) Significance

• Explain the importance of the problem or critical barrier to progress in the field that the proposed project addresses.
• Explain how the proposed project will improve scientific knowledge, technical capability, and/or clinical practice in one or more broad fields.
• Describe how the concepts, methods, technologies, treatments, services, or preventative interventions that drive this field will be changed if the proposed aims are achieved.

The problem here is the big shift in emphasis. I think I still need to provide the background information here, but it needs to be much more explicitly placed in the context of advancing the field.

(b) Innovation

• Explain how the application challenges and seeks to shift current research or clinical practice paradigms.
• Describe any novel theoretical concepts, approaches or methodologies, instrumentation or intervention(s) to be developed or used, and any advantage over existing methodologies, instrumentation or intervention(s).
• Explain any refinements, improvements, or new applications of theoretical concepts, approaches or methodologies, instrumentation or interventions.

Hmm, do I seek to shift current research paradigms??? Well yes, in overthrowing the 'transformation=sex' paradigm, but that won't be accomplished by the work proposed here. Maybe overturning the paradigm of random recombination? We will be developing novel strategies and refinements for using sequencing to study rare events, and more generally by using deep sequencing to study recombination.

C. Approach

• Describe the overall strategy, methodology, and analyses to be used to accomplish the specific aims of the project. Include how the data will be collected, analyzed, and interpreted as well as any resource sharing plans as appropriate.
• Discuss potential problems, alternative strategies, and benchmarks for success anticipated to achieve the aims.
• If the project is in the early stages of development, describe any strategy to establish feasibility, and address the management of any high risk aspects of the proposed work.
• Discuss the PD/PI's preliminary studies, data, and/or experience pertinent to this application.

OK, here's where we'll talk about what we want to accomplish. I think the order here is flexible, so we'll describe overall strategies, then preliminary data, and then the details of the research we propose.

I promised myself that I'd have a rough draft by the end of November, so I'd better get busy converting my outline into paragraphs.

Improved trait mapping?

A few weeks ago I posted the first figure below to illustrate the logic of our planned experiment to map the locations of the alleles that cause some strains of Haemophilus influenzae to transform very poorly or not at all. (Sorry, that's not an easy sentence.) The sensitivity of that experiment isn't very good. Below I'll explain why and describe what I think may be a better approach. (And the RA just suggested another approach that sounds good, so I'll try to incorporate that one too.)

First a paragraph of background. Different strains of H. influenzae differ dramatically in how well they can take up DNA and recombine it into their chromosome (their 'transformability'). Transformation frequencies range from 10^-2 to less than 10^-8. We think that finding out why will help us understand the role of DNA uptake and transformation in H. influenzae biology, and how natural selection acts on these phenotypes. Many other kinds of bacteria show similar strain-to-strain variation in transformability, so this understanding will probably apply to all transformation. The first step is identifying the genetic differences responsible for the poor transformability, but that's not so easy to do, especially if there's more than one difference in any one strain.

Step 1: The first step we planned is to incubate competent cells of the highly transformable lab strain with DNA from the other strain we're using, which transforms 1000-10000 times more poorly. We can either just pool all the cells from the experiment, or first enrich the pool for competent cells by selecting those that have acquired an antibiotic resistance allele from that DNA. We expect the poor-transformability allele or alleles from the donor cells (call them tfo- alleles) to be present in a small fraction (maybe 2%?) of the cells in this pool.

Step 2: The original plan was to then make the pooled cells competent again, and transform them with a purified DNA fragment carrying a second antibiotic resistance allele. The cells that had acquired tfo- alleles would be underrepresented among (or even absent from) the new transformants, and, when we did mega-sequencing of the DNA from these pooled second transformants, the responsible alleles would be similarly underrepresented or absent.

The problem with this plan is that it's not very sensitive. Unless we're quite lucky, detecting that specific alleles (or short segments centered on these alleles) are significantly underrepresented in the sequence will probably be quite difficult. The analysis would be much stronger if we could enrich for the alleles we want to identify, rather than depleting them. The two alternatives described below would do this.

Step 2*: First, instead of selecting in Step 2 for cells that can transform well, we might be able to screen individual colonies from Step 1 and pool those that transform badly. We have a way to do this - a single colony is sucked up into a pipette tip, briefly resuspended in medium containing antibiotic-resistant DNA, and then put on an antibiotic agar plate. Lab-strain colonies that transform normally usually give a small number of colonies, and those that transform poorly don't give any. Pooling all the colonies that give no transformants (or all the colonies that fall below some other cutoff) should dramatically enrich for the tfo- alleles, and greatly increase the sensitivity of the sequencing analysis. Instead of looking for alleles whose recombination frequency is lower than expected, we'll be looking for spikes, and we can increase the height of the spikes by increasing the stringency of our cutoff.

The difficulty with this approach will be getting a high enough stringency for the cutoff. We don't want to do the work of carefully identifying the tfo- cells, we just want to enrich for them. In principle the numbers of colonies can be optimized by varying the DNA concentration and the number of cells plated, but these tests can be fussy because the transformation frequencies of colonies on plates are hard to control.

Step 1* (the RA's suggestion): Instead of transforming the lab strain with the poorly-transforming strain in Step 1, we could do the reverse, using DNA from the lab strain and competent cells from the poorly transformable strain. Step 2 would be unchanged; we would make the pooled transformants competent and transform them with a second antibiotic-resistance marker, selecting directly for cells that have acquired this marker. This would give us a pool of cells that have acquired the alleles that make the lab strain much more transformable, and again we would identify these as spikes in the recombination frequency.

The biggest problem with this approach is that we would need to transform the poorly transformable strain. We know we can do this (it's not non-transformable), but we'd need to think carefully about the efficiency of the transformation and the confounding effect of false positives. If we include the initial selection described in Step 1, we could probably get a high enough frequency of tfo+ cells in the pool we use for step 2.

The other problem with this approach is that we'd need to first make the inverse recombination map (the 'inverse recombinome'?) for transformation of lab-strain DNA into the tfo- strain. This would take lots of sequencing, so it might be something we'd plan to defer until sequencing gets even cheaper.

I think we may want to present all of these approaches as alternatives, because we're proposing proof-of-concept work rather than the final answer. The first two are simpler and will work even on (best on?) strains that do not transform at all. The last will work very well on strains that do transform at a low frequency..

Still not done

The batch of runs in paragraph F in last night's post ran fast, but only because they were (incorrectly) set up to use a genome sequence that was only 20 kb. I forgot that they needed longer input sequences than the 20 kb of random sequence plus 100 uptake sequences I'd used for the other runs. So now I've created 50 kb, 100 kb and 200 kb versions, seeded with 250, 500 and 1000 uptake sequences respectively, and queue'd those runs.

One of the runs I thought to have hung has finished, and it gives me enough data to fix the graph I needed it for. But I'm not going to do any more work on this until my co-authors have ahd a chance to consider whether we want to include this figure (I like it).

Getting the US variation manuscript off my hands

Yesterday I gave up and sent the current version of our manuscript about uptake sequence variation off to my coauthors. I'm afraid I'd gotten caught up in generating more and more data, trying to fill gaps in the analysis, when what I really should have been doing was writing a Discussion. But the coauthors will do that, giving me a Discussion draft I can work on further. I'm hoping that they'll also come up with answers and suggestions for all (or at least most) of the issues I've raised in the other parts of the manuscript.

Below I'm going to try to summarize the new data (new simulation runs) I've generated. Right now I can't even remember what the runs were for, and I haven't properly analyzed any of them.

A. One pair of runs were two runs with 10 kb genomes that were intended to split the load of a 20 kb genome run that had stalled (needed only as one datapoint on a graph). That run had used a very low mutation rate and I was trying to run it for a million cycles, but it had stalled after 1.87x10^5 cycles. Well, it kept running, but not posting any more data so eventually I aborted it. Splitting it into two 10 kb runds didn't help - both hung after 1.87 x 10^5 cycles. Now I've made two changes. First, I've modified the 'PRINT' commands so that updates to the output file won't be stuck in the cluster's buffer; this may be why updates to the output files were so infrequent (sometimes not for weeks!). Second, I've set these runs to go for only 150,000 cycles and to report the genome sequences when they finish. This will let me use their output sequences as inputs for new runs.

B. Another pair of runs were duplicates of previous runs used to illustrate the equilibrium. One run started with a random-sequence genome and got better, the other started with a genome seeded with many perfect uptake sequences and got worse. They converge on the same final score, as seen in the figure below.

C. And one run was to correct a mistake I'd made in a 5000 cycle run that used the Neisseria meningitidis DUS matrix to specify its uptake bias. I should have set the mutation parameters and the random sequence it started with to have a base composition of 0.51 G+C, but absentmindedly used the H. influenzae value of 0.38. I needed the sequence that this run would produce, because I wanted to use the sequence outputs of it and its H. influenzae USS matrix equivalent as inputs for another 5000 cycles of evolution. I got the sequence from the first run, and started the second pair of runs, but unfortunately the computer cluster I'm using suffered a hiccup and those runs aborted. So I'll queue them again right now. (Pause while I re-queue them...)

D. Then there were four runs that used tiny fragments - enough 50, 25 and 10 bp fragments to cover 50% of the 200 kb genome. Because the length of the recombining fragments sets the minimum spacing of uptake sequences in equilibrium genomes, we expect runs using shorter fragments to give higher scores. But because the fragment mutation rate is 100-fold higher than the genomic rate in our simulations, most of the unselected mutations in our simulated genomes come in by recombination, in the sequences flanking uptake sequences. This means that genomes that recombine 10 bp fragments get few mutations outside of their uptake sequences, so I also ran the 10 bp simulation with a 10-fold higher mutation rate. These runs haven't finished yet - in fact, most of them have hardly begun after 24 hrs. I think I'd better set up new versions that use the bias-reduction feature, and then run the outputs of these in runs with unrelenting bias. (Pause again...)

The rest of the new runs were to fill in an important gap in what we'd done. The last paragraph of the Introduction promised that we would find out what conditions were necessary for molecular drive to cause accumulation of uptake sequences. But we hadn't really done that - i.e. we hadn't made an effort to pin down conditions where uptake sequences don't accumulate. Instead we'd just illustrated all the conditions where they do.

E. So one series of runs tested the effects of using lower recombination cutoffs (used with the additive versions of the matrix) when the matrix was relatively weak. I had data showing that uptake sequences didn't accumulate if the cutoff was less than 0.5, but only for the strong version of the matrix. Now I know that the same is true for the weak version.

F. Another series tested very small amounts of recombination. The lowest recombination I'd tested in the runs I had already done was 0.5% of the genome recombined each cycle, which seemed like a sensible limit as this is only one 100 bp fragment in a 20 kb genome. But this still gave substantial accumulation of uptake sequences, so now I've tested one 100 bp fragment in 50 kb, 100 kb and 200 kb genomes. I was initially surprised that the scores weren't lower, but then remembered that these scores were for the whole genome, and needed to be corrected for the longer lengths. And now I've also remembered that these analyses need to started with seeded sequences as well as random sequences, because this is the rigorous way we're identifying equilibria. (Another pause while I set up these runs and queue them...)

G. The final set of runs looked at what happens when a single large fragment (2, 5 or 10 kb) recombines into a 200 kb genome each cycle. Because there would otherwise be little mutation at positions away from uptake sequences, these runs also had a 10-fold elevated genomic mutation rate. The output genome sequences do have more uptake sequences than the initial random sequences, but the effect is quite small, and the scores for these runs were not significantly different than those for the runs described in the paragraph above, where the fragments were only 100 bp. This is expected (not that I think it through) because the only difference between the runs is that this set's fragments bring in 2-10 kb of random mutations in the DNA flanking the uptake sequence.

(I was going to add some more figures, but...)

Too many figures!

Right now the US variation manuscript has 17 figures*, every one of them close to my heart. And that's not counting the supplementary figures. I'll let my co-authors vote on which ones must go.

* A few of them are just placeholders for data I haven't finished analyzing yet.

But where's the microscope?

This is the optical tweezers setup I'll initially be working with. The microscope slide chamber is clamped to the light-coloured micromanipulator controls at the center, with a water-immersion objective lens on its right side and a light condenser on its left side. The little black and yellow tube at the back left is the infrared laser, and the tall silver strip beside it holds the photodetector that detects the laser light after it is bounced through mirrors and lenses, the slide chamber and condenser, and another mirror. The visible light source is out of view on the left, and the rightmost black thing is the visible-light camera which lets you see what you're doing, via the grey cable that connects it to a computer screen. Lying on the table in front of the camera is a slide chamber, left by one of the biophysics students who've been using this apparatus.

Preparing for optical tweezers work

I spent yesterday morning across town at the physics lab I'll be doing the optical tweezers work in, getting my hands on the equipment I'll be using. One of the many things I learned is that I need to work out the practicalities of bringing together (1) cells that are stuck onto a cover slip and (2) DNA-coated beads. I won't be using a flow-through chamber, at least not initially, but I think I have a plan that will work both for the initial troubleshooting under our own microscope and with the optical tweezers apparatus.

The chamber I'll be using is constructed by sandwiching two strips of Parafilm (thin wax) between a glass microscope slide and a glass coverslip, and then briefly heating the slide to melt the wax so it forms a tight seal along both sides of the coverslip. This creates a chamber that's about 2 cm long by 1 cm wide and about 100 nm high, open at both ends. The chamber holds about 20 µl of liquid. (Hang on, is that volume consistent with those dimensions? 1 cubic cm is 1 ml, and 100 nm is 1/100 of a cm, so yes.) Once the chamber is filled its ends are sealed with melted wax or clear nail polish.

For now let's assume that the cells will stick well to slides coated with poly-L-lysine and remain viable and able to take up DNA provided they're immersed in MIV competence solution or culture medium. And, that we can stick lots of chromosomal DNA onto the 1 micron styrene beads I'll be using. And, that once cells are attached to the coverslip the rest of the coverslip surface can be made non-sticky by a brief soak in a solution of BSA protein, so the DNA-coated beads don't also stick to the coverslip. (I'll no doubt be posting lots more about my efforts to get these steps working.)

Here's my plan. I'll first create a chamber using a coated coverslip (coating down). I'll then introduce some competent cells (in MIV) by pipeting 20 µl onto one edge (say the left edge) of the chamber. Capillary action draws this liquid into the chamber. After a few minutes I'll pipette a larger volume of BSA (in MIV) at the other end of the chamber while placing a tissue at the left edge to draw liquid out. This will create a flow of BSA solution that displaces the cell solution. I'll continue to do this until all the free cells have been washed out of the chamber, and all of the reactive poly-L-lysine has been neutralized by the BSA. Then I'll pipette the beads (in MIV) into the chamber, drawing out the unwanted BSA solution on the other side. And finally I'll dry the edges and seal the ends.

One nice feature is that I should be able to trouble shoot all of this in our own lab with our own microscope. So I can find out what concentration of cells to use, how long to allow for attachment, how much BSA to use, how much washing to get rid of the unattached cells, and how many beads to use. The final test will be whether the DNA-coated beads attach to the cells (at room temperature) but uncoated beads don't. Once I have all this working, it will be time to go back to the optical tweezers apparatus!

Faculty position cover letter Do's and Don't's

Do: Start with the big-picture question your research is investigating.

Do: Explain what distinguishes your work on regulatory protein-of-the-month from everyone else's.

Do: Recheck the final text just before you submit it.




Don't: Say that you're applying because you really want to live here.

Don't: Say that you only found out about the position because your buddy showed you the ad.

Don't: List generic research 'skills' such as gel electrophoresis, cell culture, and Microsoft Excel.

Don't: Say that you're the ideal candidate.

Don't: Say that you will happily apply your specialized techniques to any research question (i.e. you don't care about the science, you just want to play with your toys).

Don't: Give a full history of every project you've ever worked on.

Don't: Fill four pages.

Don't: Talk about your passion for research (or any other feelings).

Don't: Say you're hardworking.

Dont: Delay publishing a first-author paper on your post-doc work until you're about to apply for faculty positions.

Saved at the last minute (from the need to learn a new graphing system)

Blue screen logouts in Excel - Numbers is not the answer.

Ever since I upgraded to Snow Leopard (a couple of weeks ago), my Mac has been suffering from 'blue screen logouts', especially in Excel. The screen briefly goes blue then I'm back to the desktop with all my open applications closed (and having lost any unsaved work). The solution may be to finally switch from Office 2004 to Office 2008. I think we did buy the Office 2008 suite a couple of years ago, but maybe we only bought a one-computer version that was installed on the laptop of a post-doc who's long gone.

I've got a lot of data to analyze from all the simulations I've run, so I'm going to try using the Mac Numbers app instead. Whoa, doesn't look good. Here's what the default for a line graph produced:
Weird? Let me count the ways.

1. The background is transparent.
2. This is a 3-D graph.
3. The lines are 3-d, like ropes.
4. The lines have 3-D shadows.
   
5. There are no visible axes.
6. There is no scale.
7. There are some numbers connected to some of the lines.
8. The legend at the bottom seems to treat the X-axis values as Y-axis values.

Maybe I should have started with something simpler (this was about 15 columns of data). Now it's crawling when I just type 1, 2, 3 etc., but it speeded up when I closed the large file.
Ah, the problems with the previous graph were partly that I had accidentally chosen 3-D. But my new graph is terrible too.

1. The symbols are enormous and I can't find any way to change them or remove them.
2. My X-axis values are being treated as Y-axis values - I don't know what it's using for the X-axis as the numbers are illegibly jammed together.
3. My column headings (Cycles, Scores) are ignored.

Aha, changing to a scatter plot got it to use my Cycles data for the X-axis values. But now the lines connecting the points have disappeared and I see no way to get them back. And the new legend says that the Xs represent cycles, when they're really Scores. Instead moving the Cycles data over into the grey first column gave a semi-presentable line graph, but now it's not treating the Cycles values as numbers but as textual labels, even though I discovered how to tell it that they are numbers.

I'm afraid Numbers appears to be just a toy app, suitable for children's school projects but not for serious work. I would RTFM but I can't find anything sensible.

Uptake sequence stability

I'm back working on the US-variation manuscript. It's looking good. My coauthor's edits are useful, and she had several suggestions for relatively simple new analyses using the simulation of uptake sequence evolution.

She asked whether the positions of uptake sequences were stable once the score had reached equilibrium. Another way to say this is to ask whether the equilibrium is dynamic, with old uptake sequences lost to random mutation and new ones appearing in new places, or whether once an uptake sequence has arisen it tends to persist, presumably because mutant versions are efficiently restored by recombination. In real genomes of the same genus or family we tend to find the latter - uptake sequences are in homologous positions.

So I set up some runs that started with 200kb sequences that had evolved to equilibrium under more-or-less standard simulation conditions and would run for between 5000 and 200,000 additional cycles. The first results are done (just the 5000-cycle runs) and already the results are interesting.

The analysis will need to be redone because I'm not using the correct (10-mer) version of the US-locating perl script, but a 9-mer version intended for perfect USS cores. I'm also doing the analysis inefficiently in Excel using VLOOKUP; maybe my coauthor can write a little perl script to do it.

When the bias of the uptake machinery was fairly weak (because the matrix was applied additively), only one of the 44 perfect 9-mer uptake sequences in the input sequence was in the same location in the output sequence. But when the bias was strong (because the matrix was applied multiplicatively), 145 of the 205 original uptake sequences were present in the same positions in the output sequence.

This is a pleasing result. When the bias is strong, uptake sequences that acquire random mutations are restored by recombination before they can diverge (does this mean within a single cycle?). But when bias is weaker they often diverge before recombination can catch them. I'll have lots more data in a few days - I think some of the runs also test the effect of mutation rate.

Trait mapping

Here's the plan:

New! Improved! The NIH plan!

How's this?

Specific Aims:

Aim A. Map the H. influenzae recombinome. This is basically a higher resolution version of what we just proposed to Genome BC. We will propose to use next-gen sequencing to map the frequency of recombination at all the >40,000 SNPs and >300 indels/rearrangements between two H. influenzae strains, Rd and 86-028NP. These frequencies will be the net effects of biases at many levels of the transformation process.

Aim B. Characterize the components contributing to the recombinome of strain Rd.

1. Uptake bias (across the outer membrane)
2. Translocation biases (across the inner membrane)
3. Cytoplasmic biases (nucleases and protection)
4. Strand-exchange biases (RecA-dependence)
5. Mismatch repair biases

To do this we will use various combinations of mutants and experimental manipulations to (i) eliminate other effects and (ii) generate DNA samples enriched for the effects of the component of interest. For example, we can get a DNA sample enriched for preferred uptake sequences (step 1) by giving rec2-mutant cells synthetic degenerate uptake sequences. We can see the effects of repair (step 5) by comparing the Aim A recombinome with one produced by mismatch-repair mutants. Maybe we can detect RecA's contribution (step 4) by repeating the analysis in rec1 cells expressing the lambda bet recombinase. We can propose lots of different analyses here, giving some high priority, tagging others with 'if time and resources permit', and leaving some as 'future directions'.

Aim C. Develop a genome-wide map of genes contributing to the transformability differences between these two strains.

I don't seem to have posted about this before, and the post-doc hasn't either (it's his idea). I think it deserves a separate post. I'll just say here that this will be presented partly as a proof-of-concept study for a method that can then be used to map genes contributing to any selectable trait.

Aims B and C both depend on first completing Aim A but they are independent of each other. They also share the lovely property of being open-ended, putting us in the best version of Hershey Heaven.

Now, where was I?

Things to get back to, now the Genome BC grant is done:

Work on the US-variation manuscript: My co-author sent me her comments on the first draft a coupe of weeks ago but I have yet to read them. And I have a lot of new data from simulations that took days and weeks to run. Five more have been running for 3-4 weeks and are still not done - unfortunately I don't have a way to check how close to finishing they are. Each simulation writes very frequent updates to its output file, but but these aren't appearing in the interim copy of the file I can download. I want to get a better draft back to the co-author by the middle of the month.

Optical tweezers work: I'll make my first 'training visit' to the physics lab across town next week, so I need to at least think about what I want to accomplish. Perhaps it's time to get back in the lab and get my hands wet.

NIH proposal: We need to use the momentum from the Genome BC proposal to do serious work on our NIH proposal. It's not due until the start of February, but we need to have a reasonable draft done by Christmas. We should get our first draft done by the end of November (sooner = better).

What else? Our overall short-term plan is to focus on work that will improve the NIH proposal and (if necessary) the CIHR resubmission. The post-doc is going to work on the sample-preparation parts of the NIH work - to show that we can indeed prepare DNAs with the properties we need. The Research Associate is working on CIHR-related problems; my optical tweezers work fits this too. What can I be doing for the NIH proposal, besides writing and getting the US-variation manuscript done?

Genome BC's submission software...

...can't keep its attachments straight.

I upload the budget spreadsheet on the Budget page, but it doesn't appear there. I log out, go back, and it's now on both the Budget page and the Letters of Support page. I upload some letters of support (as pdfs), and they appear in the right place, but the Suggested Referees pdf shows up on the Budget page. Log out, log back in, now the five publication pdfs are on the Publication page, now they've been replaced by the letters of support.

I have my fingers crossed, hoping that the various uploaded pdfs actually are correctly identified in the Genome BC server, and that the screw-up is just in where it tells me they are.

We're just assembling the final big pdf of the components that are submitted as one file (Cover pages and Lay Summary and scientific Summary and Proposal and References and Figures (with the glorious Gantt chart!) and Strategic Objectives and SWOT matrix and... and ...). Then we'll try to upload it onto the appropriate page of the submission program and see what happens next.

Followup: Submission appeared to work fine. But the system doesn't give you a pdf of the total submission that you can check for errors, just a nice green checkmark, so all I can do is hope that all the components are in the right places.

Genome BC proposl angst

(In truth, I'm not even sure what 'angst' means...)

I'm alternating between thinking that our various drafts are written very bacly (so we should just abandon the proposal) and remembering that the science we propose is really dazzling. Back and forth and back and forth...

The horror!

List of all the components of our Genome BC proposal:

1. Signature page
2. Participating Organizations Signatures ( ≠ signature page)
3. Co-applicants
4. Lay summary
5. Summary
6. Proposal (5 pages, plus 5 for references, figures etc.)
7. Gantt chart (to be included with figures)
   
8. SWOT analysis matrix and explanatory statement
9. Strategic Outcomes (???)
10. Project team
11. Budget (Excel spreadsheet provided)
12. Co-funding strategy
13. Budget justification
14. Documents supporting budget justification
15. Suporting documents for co-funding
16. List of researchers on the 'team' (just me and the post-doc?)
17. Researcher profile for me
18. Researcher profile for the post-doc
19. List of collaborators and support
20. Publications (we can attach five relevant pdfs)
21. Certification forms form
22. Biohazard certification form (we're supposed to get one especially for this proposal, but only if the project is approved)

It's due Tuesday Nov. 3 (yes, the day after tomorrow!), I guess by midnight as I can't find any other time listed. I made a start at the online submission form a few days ago, but now I can log into their site but I can't access the work I've already done! There are no active links on the page that shows the application I started! (OK- solved that problem - this is some sort of Flash app, and I needed to double-click on the project title.)

limits set by sequencing errors

The post-doc and I have also been grappling with how the high error rate of the sequencing technology we'll use affects our ability to detect donor alleles in our big pool of recombinant chromosomes. Because this rate is usually about 0.5-1% per position, at positions where donor and recipient sequences have different bases, about 0.2% of the time sequencing will report a donor allele where the real molecule had a normal recipient allele. If we have 500 reads covering a position, on average one of them will appear to be a donor allele even if there has been much less than 0.2% recombination at that position. Because of random events, some positions with little or no recombination will have no sequences reporting the donor allele, but others will have 2 or 3 or more.

At face value this sets a lower limit to the rates of recombination we'll be able to detect. If a SNP position undergoes 0.1% recombination, the difference in the number of donor alleles reported will not be significantly different from the background due to error. This limit is largely independent of the amount of sequencing we do. In principle one could do enough sequencing to even out the random fluctuations in the numbers of errors seen so that a 0.1% recombination rate at a SNP position would be significantly above background, but 'enough' sequencing would be absurdly expensive.

Luckily for us, another post-doc (the clever partner of mine) has just pointed out that we can use the co-occurrence of donor alleles at adjacent SNP positions in a single sequencing read as evidence of recombination. That's because, once the software has excluded those reads whose sequences appear unreliable, we expect most single-nucleotide errors to occur independently of each other - that is, finding an error at one position does not change the probability of finding an error at another position in the same read. We can of course control for this by looking at our control sequencing of unrecombined genomes and at positions where donor and recipient are identical.

But we expect most recombination tracts to be much longer than the ~75 bp covered by a single read (we're going for these rather than the cheaper 50 bp reads). So if we see donor alleles at two SNP positions in a single read, we can be pretty sure* that they arose by one recombination event, not two coincidental sequencing errors. Of course this logic can only be applied where SNPs are close enough to be sequenced in the same read. The post-doc has now checked this, and tells me that 77% of the SNPs in the two sequences we'll use are within 50 bp of each other (the median separation is only 14 bp).

(*The limit becomes the square of the error rate, about 4 x 10^-6.)

It gets better. Because we're going to do 'paired-end' sequencing, we'll actually have two 75 bp sequences for each DNA fragment in our big recombinant pool, separated by about 400 bp of not-sequenced DNA. Provided most recombination tracts are longer than 500 bp (we expect this, and will know for sure from the clones we'll sequence), seeing donor alleles at SNP positions in both end reads will also be evidence of recombination rather than coincidental random errors.

I expect that this analysis will be a pain to do (for the post-doc, as he's the only one with the skills to do it), but it greatly improves our ability to detect low recombination frequencies.