One fof the post-docs tested the media bottles for toxic detergent residues by making one big batch of our standard BHI medium and pouring it into 20 different bottles of all the types we use for media. E. coli grew in the media from all these bottles.
I don't know whether she tested growth of H. influenzae over the weekend. If they all grew too then we have the unfortunate resolution that the problem has gone away without our ever discovering what causes it. In any case I think we're going to have our lab assistant thoroughly rinse all our bottles.
Modeling mutation with transition bias
As part of our new-improved Perl model of uptake sequence evolution, we had been intending to incorporate the usual transition:transversion bias into the part of the model that simulates mutation of the evolving sequence. But it's turning out to be HARD.
In the previous version, the mutation step incorporated a bias of the same strength as the user-specified base composition. For the H. influenzae genome (38% G+C), the routine we were using caused the mutagenesis to produce As and Ts each 31% of the time and to produce Gs and Cs each 19% of the time. This was perfectly satisfactory (or would have been if not for other components of the mutagenesis that were unnecessarily cumbersome).
At a recent planning session we thought we had figured out a way to also have transition mutations (A<->G and C<->T) occur twice as often as transversion mutations, while maintaining the specified base composition. But, when we implemented these steps into a sub-program, the base composition (initially 38%G+C) increased with each cycle of mutagenesis, leveling out at about 45% G+C. So we went back to the drawing board (the big whiteboards in the hall) and tried to understand what was wrong.
Several things were wrong. One was an error in the computer code. We fixed that, but there was another error in the implementation, so we fixed that too. Then it became clear that there was also a fundamental error in our planned steps. We had thought that we simply needed to specify the ratio of A+T to G+C and the transition bias (2-fold). But with transition bias the number of each type of mutation depends not only on the properties of the mutagenesis algorithm but on the proportions of the bases in the sequence. For example, mutagenesis of a genome with lots of As will produce more mutations to Gs than will the same mutagenesis steps acting on a genome with few As.
So I spent much of this afternoon doing algebra, trying to come up with a general relationship between the base composition bias of the mutagenesis steps and the equilibrium base composition it will produce. Unfortunately I only do algebra about once every 5 years and, although I remember the very basic rules I learned in grade 9, I have none of the skills and creativity that a regular user would have. Or maybe the problem I was trying to solve is just intrinsically messy. In any case, I covered two whiteboards with Xs and Fs and parentheses but the equations never simplified. I could call on a mathematician friend for help, or we could simply decide that incorporating a transition:transversion bias is an unnecessary refinement that actually won't make any difference to the outcome of our model.
For now we're going to take the latter approach, which will allow our programming assistant to create some working code. If we later figure out how to incorporate the transition:transversion bias, we can probably just add the necessary lines to the mutagenesis section of the program.
In the previous version, the mutation step incorporated a bias of the same strength as the user-specified base composition. For the H. influenzae genome (38% G+C), the routine we were using caused the mutagenesis to produce As and Ts each 31% of the time and to produce Gs and Cs each 19% of the time. This was perfectly satisfactory (or would have been if not for other components of the mutagenesis that were unnecessarily cumbersome).
At a recent planning session we thought we had figured out a way to also have transition mutations (A<->G and C<->T) occur twice as often as transversion mutations, while maintaining the specified base composition. But, when we implemented these steps into a sub-program, the base composition (initially 38%G+C) increased with each cycle of mutagenesis, leveling out at about 45% G+C. So we went back to the drawing board (the big whiteboards in the hall) and tried to understand what was wrong.
Several things were wrong. One was an error in the computer code. We fixed that, but there was another error in the implementation, so we fixed that too. Then it became clear that there was also a fundamental error in our planned steps. We had thought that we simply needed to specify the ratio of A+T to G+C and the transition bias (2-fold). But with transition bias the number of each type of mutation depends not only on the properties of the mutagenesis algorithm but on the proportions of the bases in the sequence. For example, mutagenesis of a genome with lots of As will produce more mutations to Gs than will the same mutagenesis steps acting on a genome with few As.
So I spent much of this afternoon doing algebra, trying to come up with a general relationship between the base composition bias of the mutagenesis steps and the equilibrium base composition it will produce. Unfortunately I only do algebra about once every 5 years and, although I remember the very basic rules I learned in grade 9, I have none of the skills and creativity that a regular user would have. Or maybe the problem I was trying to solve is just intrinsically messy. In any case, I covered two whiteboards with Xs and Fs and parentheses but the equations never simplified. I could call on a mathematician friend for help, or we could simply decide that incorporating a transition:transversion bias is an unnecessary refinement that actually won't make any difference to the outcome of our model.
For now we're going to take the latter approach, which will allow our programming assistant to create some working code. If we later figure out how to incorporate the transition:transversion bias, we can probably just add the necessary lines to the mutagenesis section of the program.
Cells are (sometimes) growing but understanding isn't
In the new batches of media I made, both H. influenzae and E. coli grew in A (our Difco BHI) and in C (borrowed BHI) and D (old HI). They didn't grow at all in B (MBP BHI). Reinoculation of media from these bottles by one of the post-docs and by me (using independent H. influenzae stocks) gave good growth in A, C and D but not B.
But there was surprising contamination in both our cultures. Surprising because previous uses of the identical stocks had no contamination, and the no-cells controls showed no contamination in two control media (indicating that my hemin and NAD supplements were uncontaminated. And an agar-plate streak of my H. influenzae inoculum showed no evidence of contamination. Even the contaminants couldn't grow in medium B, but this would make better sense if another post-doc hadn't previously found that H. influenzae grows just fine in MBP BHI.
To test whether the identify of the person doing the preparation matters, another post-doc made media that should have been identical to my new A, B, C and D. But H. influenzae grew in all of these batches, even the MBP BHI. We can now (almost) conclude that growth results are reproducible for any specific bottle of media we prepare, but not for different preparations made from the same powder. (I write 'almost' because of a couple of pesky exceptions observed last week.)
I'm wondering if there's something wrong with our clean bottles....
But there was surprising contamination in both our cultures. Surprising because previous uses of the identical stocks had no contamination, and the no-cells controls showed no contamination in two control media (indicating that my hemin and NAD supplements were uncontaminated. And an agar-plate streak of my H. influenzae inoculum showed no evidence of contamination. Even the contaminants couldn't grow in medium B, but this would make better sense if another post-doc hadn't previously found that H. influenzae grows just fine in MBP BHI.
To test whether the identify of the person doing the preparation matters, another post-doc made media that should have been identical to my new A, B, C and D. But H. influenzae grew in all of these batches, even the MBP BHI. We can now (almost) conclude that growth results are reproducible for any specific bottle of media we prepare, but not for different preparations made from the same powder. (I write 'almost' because of a couple of pesky exceptions observed last week.)
I'm wondering if there's something wrong with our clean bottles....
Cells are growing but we don't know why
The dilution test showed that adding as little as one part sBHI to 4 parts sLB was enough to prevent H. influenzae cells from growing. The plating test showed that H. influenzae cells would form colonies on the surface of an sBHI agar plate, but wold not form colonies if they are embedded in a layer of sBHI top agar. None of these results make any sense.
So we decided to go back and retest all the variables, in the assumption that at least one of our previous tests gave a misleading result. The first thing to retest was the effect of different sources of BHI powder, because this is the most likely culprit. We have (A) the Difco/Bacto stock we've been using (a nearly-empty 2.5kg tub), (B) a newly opened bottle of Marine BioProducts brand, and (C) a Difco BHI bottle from another lab (dated 2003). We also have (D) an ancient bottle of Difco heart infusion powder (HI) that I bought when I started the lab in 1990 but never opened.
I made 200 ml of each, weighing the powder directly into the bottle (no weighboat) and filling the bottle directly from the water carboy (no measuring cylinder). I inoculated 5 ml of each with 200 ul of H. influenzae cells from the LB overnight. As controls I used the reproducibly toxic BHI stock E I had been previously using, and the LB that the cells reproducibly grew in.
After a few hours it was clear that the cells were growing slowly in medium A, faster in media C, D and LB, and not at all in B and E. The growth in A is unexpected, as A should be identical to E. We also inoculated E. coli into these media - we'll see the growth results this morning.
So we decided to go back and retest all the variables, in the assumption that at least one of our previous tests gave a misleading result. The first thing to retest was the effect of different sources of BHI powder, because this is the most likely culprit. We have (A) the Difco/Bacto stock we've been using (a nearly-empty 2.5kg tub), (B) a newly opened bottle of Marine BioProducts brand, and (C) a Difco BHI bottle from another lab (dated 2003). We also have (D) an ancient bottle of Difco heart infusion powder (HI) that I bought when I started the lab in 1990 but never opened.
I made 200 ml of each, weighing the powder directly into the bottle (no weighboat) and filling the bottle directly from the water carboy (no measuring cylinder). I inoculated 5 ml of each with 200 ul of H. influenzae cells from the LB overnight. As controls I used the reproducibly toxic BHI stock E I had been previously using, and the LB that the cells reproducibly grew in.
After a few hours it was clear that the cells were growing slowly in medium A, faster in media C, D and LB, and not at all in B and E. The growth in A is unexpected, as A should be identical to E. We also inoculated E. coli into these media - we'll see the growth results this morning.
Not the size of the inoculum, and not the water...
I tested the effect of inoculum size by trying to grow serial dilutions of both E. coli and H. influenzae in a variety of media, with 10-fold dilutions ranging from 10^-2 to 10^-9 of a turbid resuspension. All of the E. coli dilutions grew fine in LB and none grew in BHI or sBHI (testing the effect of hemin and NAD on E. coli in BHI). And all of the H. influenzae dilutions grew fine in sLB but not at all in sBHI. So the growth failure doesn't depend on the number of cells inoculated.
So today we made up BHI using water obtained from various other labs nearby (labs with fancy water-purification systems) and from tap water. None supported growth of H. influenzae, and they only weakly supported growth of E. coli. Because I had realized that the LB that always supported growth had been made up about 6 weeks ago, we also made fresh LB with our current stock of distilled water. It supported growth just as well as the old LB. So the problem isn't something in our water.
My tests of the different agar plates confirmed that media that doesn't support growth in broth does support growth just fine when solidified with agar. And plating of the previous day's E. coli 'didn't grow' cultures showed that the broth contained about 10^6 cfu/ml, which is not very different from the cfu it was inoculated with.
One of the post-docs has set up a test of whether the growth state of the inoculated cells matters. She took H. influenzae cells left from last-night's test (the same ones that failed to grow in the various water tests but did grow in sLB), and from the newly-growing sLB culture.
I've now set up overnight tests of whether the agar-solidified medium supports H. influenzae growth if the cells are embedded in a layer of top agar (more dilute agar) on top of the sBHI, or are embedded in 10ml of sBHI agar. I tested both top agar made with medium E and made with half medium E and half LB.
And to test whether added sLB restores growth to H. influenzae cells in sBHI, or whether added sBHI poisons cells in sLB, I've inoculated cells into various mixtures (5:0, 4:1, 3:2, 2:3, 1:4, 0:5).
The situation is getting scary, as we're fast running out of variables to test.
So today we made up BHI using water obtained from various other labs nearby (labs with fancy water-purification systems) and from tap water. None supported growth of H. influenzae, and they only weakly supported growth of E. coli. Because I had realized that the LB that always supported growth had been made up about 6 weeks ago, we also made fresh LB with our current stock of distilled water. It supported growth just as well as the old LB. So the problem isn't something in our water.
My tests of the different agar plates confirmed that media that doesn't support growth in broth does support growth just fine when solidified with agar. And plating of the previous day's E. coli 'didn't grow' cultures showed that the broth contained about 10^6 cfu/ml, which is not very different from the cfu it was inoculated with.
One of the post-docs has set up a test of whether the growth state of the inoculated cells matters. She took H. influenzae cells left from last-night's test (the same ones that failed to grow in the various water tests but did grow in sLB), and from the newly-growing sLB culture.
I've now set up overnight tests of whether the agar-solidified medium supports H. influenzae growth if the cells are embedded in a layer of top agar (more dilute agar) on top of the sBHI, or are embedded in 10ml of sBHI agar. I tested both top agar made with medium E and made with half medium E and half LB.
And to test whether added sLB restores growth to H. influenzae cells in sBHI, or whether added sBHI poisons cells in sLB, I've inoculated cells into various mixtures (5:0, 4:1, 3:2, 2:3, 1:4, 0:5).
The situation is getting scary, as we're fast running out of variables to test.
Curiouser and curiouser
So yesterday I did almost exactly the same test of medium A I had done the day before. The H. influenzae results were the same - cells grew in sLB but not in sBHI. But this time the E. coli didn't grow in sBHI either (it did grow in sLB), whereas yesterday it had grown well in both media. The growth/no growth distinctions were made by both microscopic examinations and turbidity checks. This confirms that the post-docs' earlier result of E. coli sometimes not growing in sBHI was not due to something odd they had done on that day. So whatever the problem is, it can affect both E. coli and H. influenzae.
The only differences I'm aware of are that I inoculated the cultures with fewer cells (both E. coli and H. influenzae), and, it being a different day, I used cells taken from newly grown colonies on agar plates. I had the same results with the other batches of media the post-docs had tested (B, C and D), as did the post-docs. And I had the same result with medium batch E, freshly prepared by one of the post-docs.
I also tested survival of the cells by plating the inoculum (H. influenzae only) before it was added to the test media, and the cultures at different times (H. influenzae after 30 minutes and 3 hours, and E. coli after 3 hours). I used both old plates that were known to work fine and new plates made with batch E BHI, so this will also tell me whether the problem occurs only in liquid medium.
Today I'm going to test whether the size of the inoculum makes a difference. This will require lots of plates, so I hope the test batch E plates worked fine. It would be hard to do this test properly using just the microscope and turbidity checks. Inoculum size can make a difference - I remember once when we had to use a borrowed shaker for our culture tubes (our roller wheel being broken) we found that a too-small inoculum of H. influenzae gave no growth in sBHI. It was as if the medium contained a limited amount of something toxic that was removed from the medium when it was absorbed by the cells, so that when only few cells were present each received a toxic dose of this hypothetical substance, whereas when more cells were present each received a proportionally smaller and thus non-toxic dose. We didn't bother tracking down this mystery because we stopped using the borrowed shaker as soon as our roller wheel was fixed.
The plating I've done should tell me whether the BHI kills the cells or just doesn't allow them to grow. I may also do the 50:50 (sLB:sBHI) mixing test, which I didn't have time to do yesterday - maybe even testing different ratios of the two media.
I may also seek out another source of pure water (from another lab), just in case something has gone weird with either our still or the carboys we store its output in.
The only differences I'm aware of are that I inoculated the cultures with fewer cells (both E. coli and H. influenzae), and, it being a different day, I used cells taken from newly grown colonies on agar plates. I had the same results with the other batches of media the post-docs had tested (B, C and D), as did the post-docs. And I had the same result with medium batch E, freshly prepared by one of the post-docs.
I also tested survival of the cells by plating the inoculum (H. influenzae only) before it was added to the test media, and the cultures at different times (H. influenzae after 30 minutes and 3 hours, and E. coli after 3 hours). I used both old plates that were known to work fine and new plates made with batch E BHI, so this will also tell me whether the problem occurs only in liquid medium.
Today I'm going to test whether the size of the inoculum makes a difference. This will require lots of plates, so I hope the test batch E plates worked fine. It would be hard to do this test properly using just the microscope and turbidity checks. Inoculum size can make a difference - I remember once when we had to use a borrowed shaker for our culture tubes (our roller wheel being broken) we found that a too-small inoculum of H. influenzae gave no growth in sBHI. It was as if the medium contained a limited amount of something toxic that was removed from the medium when it was absorbed by the cells, so that when only few cells were present each received a toxic dose of this hypothetical substance, whereas when more cells were present each received a proportionally smaller and thus non-toxic dose. We didn't bother tracking down this mystery because we stopped using the borrowed shaker as soon as our roller wheel was fixed.
The plating I've done should tell me whether the BHI kills the cells or just doesn't allow them to grow. I may also do the 50:50 (sLB:sBHI) mixing test, which I didn't have time to do yesterday - maybe even testing different ratios of the two media.
I may also seek out another source of pure water (from another lab), just in case something has gone weird with either our still or the carboys we store its output in.
BHI problems
Yesterday one of the post-docs took me through the various tests they'd done trying to find out what's wrong with our brain-heart infusion medium (BHI).
First some background: The standard procedure is to supplement BHI with hemin and NAD from stock supplies that are already made up to standard concentrations (giving sBHI), to put 5ml of sBHI into a 25ml glass culture tube, to add H. influenzae cells either from a frozen stock or a previous culture (usually a 1/100 dilution), and to incubate the culture overnight on a roller wheel in the 37°C incubator. H. influenzae will normally also grow in the E. coli medium LB, provided it has been supplemented with hemin and NAD (sLB). E. coli doesn't need hemin or NAD and will grow well in both LB and BHI, better in BHI because it's a richer (and more expensive) medium. Growth can be checked various ways. The easiest is simply looking at the turbidity of the culture, but we can also measure the turbidity in a spectrophotometer, dilute the culture and plate the cells on agar to count the colonies, or look at the cells under a microscope. The last is not very useful for H. influenzae, mainly because the cells are so tiny but partly because our very expensive microscope is badly out of alignment. (We are arranging for a long-overdue visit from the serviceman.)
The first tests, done with the original problematic batch of BHI, found that inoculation of sBHI culture tubes with H. influenzae produced no growth but inoculation of E. coli directly into the bottles of BHI produced abundant growth.
The lab assistant then made four bottles of new BHI using combinations of the two stocks of BHI powder (old Difco brand and new MBL brand) and two sources of distilled water (secondary carboy and source carboy); this gave four bottles, labeled A, B, C, and D. One of the post-docs supervised this to make sure she wasn't making any errors. The post-docs then inoculated tubes of these media with H. influenzae from a freezer stock (amounts not carefully controlled, and with E. coli from a fresh culture. All of the H. influenzae tubes grew but none of the E. coli ones did! They then inoculated H. influenzae from the tubes that had grown into fresh tubes of media A-D, and this time the cells didn't grow!
I wanted to find out what the medium was doing to the cells by looking at them under the microscope. So yesterday I inoculated tubes of sBHI (from bottle A) and sLB with measured amounts of H. influenzae and of E. coli. Both inocula were prepared by resuspending cells taken from fresh colonies on plates into a small amount of LB, and then adding 50 microliters to 2.5ml of medium. I used disposable plastic culture tubes rather than our standard glass culture tubes because we wanted to exclude the possibility that dirty tubes were causing the problem.
I looked at the cells immediately after inoculation and after 30', 60' and 120' in the incubator. The E. coli cells in both sLB and sBHI did what healthy cells do - they gradually became longer and divided so that, after 120' the culture was very cloudy and each microscope 'field of view' contained 5-10 times more cells than it had at the start. The H. influenzae cells in sLB also grew. Because they're so little they looked like tiny specks and threads, but the number and proportion of threads got higher, indicating that the cells were elongating and dividing into new cells. But the cells in sBHI just sat there, continuing to look like a mixture of specks and short threads. The post-doc measured the culture turbidities in the spectrophotometer, confirming that E. coli was at high density in both media (higher density in the sBHI) and that H. influenzae was at higher density in sLB than in sBHI.
What did I learn? First, the problem is reproducible. Second, it isn't dirty culture tubes. Third, the problem manifests itself quite quickly. It isn't that the cells grow initially and then run out of some key nutrient - rather they don't grow at all. Fourth, the problem isn't the hemin or NAD. These results reinforce my notion that we should focus on the inability of H. influenzae to grow in BHI medium that does allow growth of E. coli, and not worry for now about the time when H. influenzae did grow and E. coli didn't.
So what will I do today? The post-doc made a big batch of BHI and BHI agar yesterday for me to do tests with, and streaked out H. influenzae and E. coli on agar plates.
First some background: The standard procedure is to supplement BHI with hemin and NAD from stock supplies that are already made up to standard concentrations (giving sBHI), to put 5ml of sBHI into a 25ml glass culture tube, to add H. influenzae cells either from a frozen stock or a previous culture (usually a 1/100 dilution), and to incubate the culture overnight on a roller wheel in the 37°C incubator. H. influenzae will normally also grow in the E. coli medium LB, provided it has been supplemented with hemin and NAD (sLB). E. coli doesn't need hemin or NAD and will grow well in both LB and BHI, better in BHI because it's a richer (and more expensive) medium. Growth can be checked various ways. The easiest is simply looking at the turbidity of the culture, but we can also measure the turbidity in a spectrophotometer, dilute the culture and plate the cells on agar to count the colonies, or look at the cells under a microscope. The last is not very useful for H. influenzae, mainly because the cells are so tiny but partly because our very expensive microscope is badly out of alignment. (We are arranging for a long-overdue visit from the serviceman.)
The first tests, done with the original problematic batch of BHI, found that inoculation of sBHI culture tubes with H. influenzae produced no growth but inoculation of E. coli directly into the bottles of BHI produced abundant growth.
The lab assistant then made four bottles of new BHI using combinations of the two stocks of BHI powder (old Difco brand and new MBL brand) and two sources of distilled water (secondary carboy and source carboy); this gave four bottles, labeled A, B, C, and D. One of the post-docs supervised this to make sure she wasn't making any errors. The post-docs then inoculated tubes of these media with H. influenzae from a freezer stock (amounts not carefully controlled, and with E. coli from a fresh culture. All of the H. influenzae tubes grew but none of the E. coli ones did! They then inoculated H. influenzae from the tubes that had grown into fresh tubes of media A-D, and this time the cells didn't grow!
I wanted to find out what the medium was doing to the cells by looking at them under the microscope. So yesterday I inoculated tubes of sBHI (from bottle A) and sLB with measured amounts of H. influenzae and of E. coli. Both inocula were prepared by resuspending cells taken from fresh colonies on plates into a small amount of LB, and then adding 50 microliters to 2.5ml of medium. I used disposable plastic culture tubes rather than our standard glass culture tubes because we wanted to exclude the possibility that dirty tubes were causing the problem.
I looked at the cells immediately after inoculation and after 30', 60' and 120' in the incubator. The E. coli cells in both sLB and sBHI did what healthy cells do - they gradually became longer and divided so that, after 120' the culture was very cloudy and each microscope 'field of view' contained 5-10 times more cells than it had at the start. The H. influenzae cells in sLB also grew. Because they're so little they looked like tiny specks and threads, but the number and proportion of threads got higher, indicating that the cells were elongating and dividing into new cells. But the cells in sBHI just sat there, continuing to look like a mixture of specks and short threads. The post-doc measured the culture turbidities in the spectrophotometer, confirming that E. coli was at high density in both media (higher density in the sBHI) and that H. influenzae was at higher density in sLB than in sBHI.
What did I learn? First, the problem is reproducible. Second, it isn't dirty culture tubes. Third, the problem manifests itself quite quickly. It isn't that the cells grow initially and then run out of some key nutrient - rather they don't grow at all. Fourth, the problem isn't the hemin or NAD. These results reinforce my notion that we should focus on the inability of H. influenzae to grow in BHI medium that does allow growth of E. coli, and not worry for now about the time when H. influenzae did grow and E. coli didn't.
So what will I do today? The post-doc made a big batch of BHI and BHI agar yesterday for me to do tests with, and streaked out H. influenzae and E. coli on agar plates.
- I think I'll first repeat yesterday's experiment with media A-D and the new batch (call it E), this time measuring the turbidities of all cultures at the start as well as after 2 hours.
- I'll also use oil-immersion to look at the H. influenzae cells under the microscope - this is a bit more hassle but gives higher resolution.
- I'll also dilute and plate the H. influenzae cells that are in the medium they wouldn't grow in yesterday. By doing this I can find out whether the cells die (and how quickly) or just fail to grow. Finding that the cells die would suggest that the medium contains something toxic, whereas finding that they just fail to grow would suggest that the medium is lacking an important nutrient.
- I'll also try mixing the sBHI 50:50 with LB. This might also show whether there's something missing from the BHI (if H. influenzae grows in the mixture) or something toxic in the BHI (if H. influenzae doesn't grow in the mixture).
- The batch E BHI agar was made with the same medium as batch E broth, so I'll pour plates of this and see if cells grow into colonies overnight. So far the problem has been found only with cells in liquid culture, but the liquid medium and agar have been from batches made on different days. (I can do my other plating on another batch of plates that one of the post-docs poured on Monday - we know cells do grow into colonies on these plates.)
Why has our culture medium suddenly become toxic?!?
This week we're wrestling with a practical mystery - for unknown reasons the 'brain heart infusion' culture medium we usually use for H. influenzae no longer supports growth.
The problem first surfaced on Monday, when one of the post-docs found that cultures she had inoculated the night before had no growth. Suspecting that she'd made a mistake, she carefully reinoculated them, only to find no growth again on Tuesday morning. On Wednesday another post-doc found that her cultures hadn't grown either.
The medium had been prepared by our new lab assistant, so naturally we wondered if she'd made a mistake. This seemed unlikely because (1) she's very careful, and (2) making it is very simple (just dissolve 37 g of BHI powder in 1 liter of water, pour it into bottles and autoclave, and (3) the medium looked pretty normal (clear, golden brown) and we had a hard time imagining what could entirely prevent bacteria from growing in it. When she came in she confirmed that the medium had been made from the nearly-empty container of Difco BHI powder we've been using for months now, not the other-brand bottle we were going to try out someday soon.
A measuring error might have given less growth, but not none. Making the medium up with the 'wrong' water shouldn't have mattered - I'm pretty sure cells would grow fine even if the medium was made with plain tap water instead of the distilled water we meticulously use. The usual supplements of hemin and NAD were from stock tubes that had worked fine in previous cultures.
Simple tests didn't find a problem - the BHI smelled normal, and had a reasonable pH of about 8. The post-docs tried inoculating E. coli into it (less fussy than H. influenzae), but these cells didn't grow either. As well as inoculating the E. coli into 5ml of BHI in our usual culture tubes they also cleverly tried inoculating it directly into the stock bottle, and surprisingly these cells grew fine. So they suspected that maybe the problem was with the culture tubes rather than the BHI. In a parallel test they had made a fresh batch of BHI, and tested this in culture tubes with H. influenzae and E. coli. This time the E. coli again didn't grow, but the H. influenzae did, again directing suspicion to the culture tubes.
They did some more tests yesterday, so maybe today we'll figure out what the problem is...
The problem first surfaced on Monday, when one of the post-docs found that cultures she had inoculated the night before had no growth. Suspecting that she'd made a mistake, she carefully reinoculated them, only to find no growth again on Tuesday morning. On Wednesday another post-doc found that her cultures hadn't grown either.
The medium had been prepared by our new lab assistant, so naturally we wondered if she'd made a mistake. This seemed unlikely because (1) she's very careful, and (2) making it is very simple (just dissolve 37 g of BHI powder in 1 liter of water, pour it into bottles and autoclave, and (3) the medium looked pretty normal (clear, golden brown) and we had a hard time imagining what could entirely prevent bacteria from growing in it. When she came in she confirmed that the medium had been made from the nearly-empty container of Difco BHI powder we've been using for months now, not the other-brand bottle we were going to try out someday soon.
A measuring error might have given less growth, but not none. Making the medium up with the 'wrong' water shouldn't have mattered - I'm pretty sure cells would grow fine even if the medium was made with plain tap water instead of the distilled water we meticulously use. The usual supplements of hemin and NAD were from stock tubes that had worked fine in previous cultures.
Simple tests didn't find a problem - the BHI smelled normal, and had a reasonable pH of about 8. The post-docs tried inoculating E. coli into it (less fussy than H. influenzae), but these cells didn't grow either. As well as inoculating the E. coli into 5ml of BHI in our usual culture tubes they also cleverly tried inoculating it directly into the stock bottle, and surprisingly these cells grew fine. So they suspected that maybe the problem was with the culture tubes rather than the BHI. In a parallel test they had made a fresh batch of BHI, and tested this in culture tubes with H. influenzae and E. coli. This time the E. coli again didn't grow, but the H. influenzae did, again directing suspicion to the culture tubes.
They did some more tests yesterday, so maybe today we'll figure out what the problem is...
The sxy manuscript is done!
The long gestation period of our sxy manuscript is finally over. It's been accepted, we sent in the signed open access forms, and yesterday we sent our corrections to the proofs back to the copy editors. So it should appear soon on the Advance Access page of Nucleic Acids Research.
This first results reported by this paper (the existence of sxy mutations that might cause hypercompetence by disrupting base pairing in sxy mRNA) were generated about 12 years ago. If we'd properly gotten our act together we could have published a less thorough analysis a long time ago. But we didn't, for various reasons, and I'm happy they're finally appearing in such a fine paper.
This first results reported by this paper (the existence of sxy mutations that might cause hypercompetence by disrupting base pairing in sxy mRNA) were generated about 12 years ago. If we'd properly gotten our act together we could have published a less thorough analysis a long time ago. But we didn't, for various reasons, and I'm happy they're finally appearing in such a fine paper.
Anaerobically grown Bacillus need to eat DNA
I've stumbled across a paper that came out three years ago. Its title is "Anaerobic growth of Bacillus mojavensis and Bacillus subtilis requires deoxyribonucleosides or DNA", by Folmsbee, McInerney and Nagle (2004, Applied and Environmental Microbiology 70:5252-5257).
It turns out that B. subtilis and B. mohavensis grown without oxygen can synthesize ribonucleotides but can't convert them into deoxyribonucleotides, because their ribonucleotide reductase enzyme needs oxygen to remove the oxygen from ribose, converting it to deoxyribose (this seems backwards, but trust me). You can't just feed them deoxyribose, because they can't add it to bases. You can feed them deoxyribonucleosides (deoxyribose plus base) because they have specific kinases that put phosphates onto deoxynucleosides. Or you can give them DNA. Salmon sperm DNA, E. coli DNA, synthetic DNA, it all works fine. One microgram DNA/ml increases growth about 20-fold. The DNA can't replace sugar in the medium so the cells aren't using it as an energy source (i.e. they're not burning the DNA for fuel), they're just using it as building blocks for their own chromosome replication.
Is 1 microgram/ml enough to grow lots of B. subtilis cells? Back of the envelope calculation: say 1 cell/5000kb x 10^12 kb/microgram x 1 microgram/ml = 2 x 10^8 cells/ml. Yes, that's just about right.
The authors see no problem with cells using DNA as food; they're microbial physiologists and engineers, and apparently haven't been indoctrinated with the dogma that DNA can only provide genetic information. They write:
It turns out that B. subtilis and B. mohavensis grown without oxygen can synthesize ribonucleotides but can't convert them into deoxyribonucleotides, because their ribonucleotide reductase enzyme needs oxygen to remove the oxygen from ribose, converting it to deoxyribose (this seems backwards, but trust me). You can't just feed them deoxyribose, because they can't add it to bases. You can feed them deoxyribonucleosides (deoxyribose plus base) because they have specific kinases that put phosphates onto deoxynucleosides. Or you can give them DNA. Salmon sperm DNA, E. coli DNA, synthetic DNA, it all works fine. One microgram DNA/ml increases growth about 20-fold. The DNA can't replace sugar in the medium so the cells aren't using it as an energy source (i.e. they're not burning the DNA for fuel), they're just using it as building blocks for their own chromosome replication.
Is 1 microgram/ml enough to grow lots of B. subtilis cells? Back of the envelope calculation: say 1 cell/5000kb x 10^12 kb/microgram x 1 microgram/ml = 2 x 10^8 cells/ml. Yes, that's just about right.
The authors see no problem with cells using DNA as food; they're microbial physiologists and engineers, and apparently haven't been indoctrinated with the dogma that DNA can only provide genetic information. They write:
"The requirement of some Bacillus strains for DNA or deoxyribonucleosides for anaerobic growth should not be unexpected given their ability to uptake DNA by way of the competence system (7). Also, B. subtilis can cannibalize sibling cells (12), which prevents sporulation during transient periods of nutrient starvation. The nutrients released from lysed cells would include DNA and/or deoxyribonucleosides that could be used as nutrients. Thus, it is likely that some bacilli would have evolved the ability to utilize DNA or deonyribonucleosides as a nutrient source."The situation is different in E. coli. You can't feed them deoxyribonucleosides because they don't have the requisite kinases, and you can't just feed them deoxyribonucleotides because they have to strip the phosphate off (converting them to deoxyribonucloesides) to get them across the membrane. But E. coli has another ribonucleotide reductase, one that doesn't need oxygen, so it can always make the deoxyribonucleotides it needs from the ribonucleotides it synthesizes. Most other bacteria, including H. influenzae and some isolates of B. subtilis, also have this anaerobic ribonucleotide reductase.
Bacillus? Acinetobacter? Thermus?!?
I'm leaning towards doing the experiment that tests whether competent bacteria benefit nutritionally from the DNA they take up. There are two main issues to resolve. First is the design of the experiment, second is which organism to use.
I was originally thinking of simply measuring cell growth in medium with and without added DNA. This will work only if the effect of DNA is large. For it to be large, the cells will need to take up quite a lot of DNA while they are growing. If they only take up DNA when they run out of other nutrients, the effect is likely to be quite small. I would need to measure differences in growth or survival over long periods in stationary phase, rather like what Steve Finkel has done with E. coli.
An alternative to growth experiments is measuring competition. This would involve mixing cells that can take up DNA with cells that can't (probably cells with a knockout in a DNA uptake gene), and growing them in medium with and without DNA. This growth could be done over multiple dilution/growth cycles, potentially amplifying any advantage of DNA uptake. Using a non-competent mutant provides a nice internal control, but it's important that the mutation not reduce growth under conditions where DNA is not available. A minor effect might be acceptable, but I don't want to have to use statistical wizardry to show the effect of DNA.
What bacteria should this be done with? I wouldn't use H. influenzae - their nutritional requirements are too complex and the uptake specificity is a big complication. My first thought was Bacillus subtilis. I've worked with them before, and they are easy to make competent and can be grown on very simple defined media. So I spent much of yesterday reading papers about the regulation of competence in B. subtilis.
What a regulatory nightmare! I don't know whether B. subtilis gene regulation is intrinsically complex or whether the people who work on it just delight in digging up more complexities, but nobody seems to be trying to make functional sense of it. They do propose some absurd evolutionary just-so stories, such as that B. subtilis has prophage in its genome so cells can lyse under stressed conditions, allowing other cells to take up their genes.
Competence in B. subtilis is a bit of a phenotypic nightmare too - when food runs out most of the culture forms spores but about 10% of the cells instead become competent. While competent they're unable to replicate their DNA (I think) or septate their cells, so they grow into long filaments that divide into many short cells once the competence fit has passed (I saw the movie so I know this is true). Nobody who works on B. subtilis competence seems concerned by this....
I had already known about most of the B. subtilis complications (though not the DNA replication/septation arrest), but being reminded of them made me start thinking about alternatives. The first I thought of was Acinetobacter. These guys are easy to grow and nutritionally simple, like B. subtilis. Their competence development appears to be a lot simpler - there's no sporulation involved. Cells in lab culture express all the competence genes when they get into stationary phase, but they can't actually take up DNA until they're diluted into fresh medium. Then they gradually lose competence during exponential growth. This would make them quite suitable for a multi-cycle competition experiment.
But while reading about Acinetobacter I was reminded about competence in Thermus thermophilus. In lab culture these cells take up DNA all the time (less in stationary phase), giving transformation frequencies of about 1% for most genes. This might give a growth advantage large enough to be detected in a single-step growth experiment. Mutants carrying knockouts of DNA-uptake genes are readily available and well characterized. I think T. thermophilus's nutritional requirements are quite simple, but growing it is likely to be complicated because it's a hyperthermophile - lab cultures are usually grown at 60-70°C! We do have a spare shaking waterbath that could be set this high, but for competence assays and cell counts we'd want to grow cells on solid medium, and I don't even know if one can use agar at this temperature.
I'm going to email the T. thermophilus expert (Beate Averhoff, in Frankfurt) asking if she can send me a pdf of a recent chapter she wrote for a methods book (our library doesn't have it), and whether she thinks it's easy to work with.
I was originally thinking of simply measuring cell growth in medium with and without added DNA. This will work only if the effect of DNA is large. For it to be large, the cells will need to take up quite a lot of DNA while they are growing. If they only take up DNA when they run out of other nutrients, the effect is likely to be quite small. I would need to measure differences in growth or survival over long periods in stationary phase, rather like what Steve Finkel has done with E. coli.
An alternative to growth experiments is measuring competition. This would involve mixing cells that can take up DNA with cells that can't (probably cells with a knockout in a DNA uptake gene), and growing them in medium with and without DNA. This growth could be done over multiple dilution/growth cycles, potentially amplifying any advantage of DNA uptake. Using a non-competent mutant provides a nice internal control, but it's important that the mutation not reduce growth under conditions where DNA is not available. A minor effect might be acceptable, but I don't want to have to use statistical wizardry to show the effect of DNA.
What bacteria should this be done with? I wouldn't use H. influenzae - their nutritional requirements are too complex and the uptake specificity is a big complication. My first thought was Bacillus subtilis. I've worked with them before, and they are easy to make competent and can be grown on very simple defined media. So I spent much of yesterday reading papers about the regulation of competence in B. subtilis.
What a regulatory nightmare! I don't know whether B. subtilis gene regulation is intrinsically complex or whether the people who work on it just delight in digging up more complexities, but nobody seems to be trying to make functional sense of it. They do propose some absurd evolutionary just-so stories, such as that B. subtilis has prophage in its genome so cells can lyse under stressed conditions, allowing other cells to take up their genes.
Competence in B. subtilis is a bit of a phenotypic nightmare too - when food runs out most of the culture forms spores but about 10% of the cells instead become competent. While competent they're unable to replicate their DNA (I think) or septate their cells, so they grow into long filaments that divide into many short cells once the competence fit has passed (I saw the movie so I know this is true). Nobody who works on B. subtilis competence seems concerned by this....
I had already known about most of the B. subtilis complications (though not the DNA replication/septation arrest), but being reminded of them made me start thinking about alternatives. The first I thought of was Acinetobacter. These guys are easy to grow and nutritionally simple, like B. subtilis. Their competence development appears to be a lot simpler - there's no sporulation involved. Cells in lab culture express all the competence genes when they get into stationary phase, but they can't actually take up DNA until they're diluted into fresh medium. Then they gradually lose competence during exponential growth. This would make them quite suitable for a multi-cycle competition experiment.
But while reading about Acinetobacter I was reminded about competence in Thermus thermophilus. In lab culture these cells take up DNA all the time (less in stationary phase), giving transformation frequencies of about 1% for most genes. This might give a growth advantage large enough to be detected in a single-step growth experiment. Mutants carrying knockouts of DNA-uptake genes are readily available and well characterized. I think T. thermophilus's nutritional requirements are quite simple, but growing it is likely to be complicated because it's a hyperthermophile - lab cultures are usually grown at 60-70°C! We do have a spare shaking waterbath that could be set this high, but for competence assays and cell counts we'd want to grow cells on solid medium, and I don't even know if one can use agar at this temperature.
I'm going to email the T. thermophilus expert (Beate Averhoff, in Frankfurt) asking if she can send me a pdf of a recent chapter she wrote for a methods book (our library doesn't have it), and whether she thinks it's easy to work with.
Time to get back to experiments
I seem to have run out of urgent desk-work (or my brain has conveniently forgotten what remains to be done) so I'm going to get back to the bench and do an experiment or two. What should I do?
Maybe I should test whether lab cultures of Bacillus subtilis grow better if given DNA they can use as a nutrient. I briefly posted about this last month. Or maybe I should try to find out whether the H. influenzae rec-2 gene is indeed regulated by the PurR repressor. Or get back to trying to find the conditions that cause E. coli to express its sxy gene and (we predict) become naturally competent. Or, farther back, continue last spring's preparations for laser-tweezers analysis of DNA uptake by H. influenzae.
Maybe I should test whether lab cultures of Bacillus subtilis grow better if given DNA they can use as a nutrient. I briefly posted about this last month. Or maybe I should try to find out whether the H. influenzae rec-2 gene is indeed regulated by the PurR repressor. Or get back to trying to find the conditions that cause E. coli to express its sxy gene and (we predict) become naturally competent. Or, farther back, continue last spring's preparations for laser-tweezers analysis of DNA uptake by H. influenzae.
Erroneous old dprA data
A few days ago I posted an old graph of transformation data that appeared to show that the DNA-protection gene dprA was not needed in cells whose recBC gene was knocked out. This was a result I didn't remember getting, so I was going to search through my old notebook (2003-04) to see if this was a real result.
This experiment turned out to not be in my notebook because it was done by an undergraduate working in the lab. She did good work, but I can't find her lab notes on our shelf of old notebooks. (I hereby vow to work with our new lab assistant to get these notebooks better labeled and organized.) My notes of her lab meeting presentations and other discussions don't directly address this point.
But I gradually remembered that her initial results had been wrong (maybe that the strain she thought was a double dprA recBC mutant was actually only a single recBC mutant?), and that correcting the error had eliminated this interesting result, replacing it with a more solid but less interesting one. I did find a copy of her final report . It shows clearly that the double mutant had the same transformation phenotype as the single dprA mutant, so she concluded that DprA's job is not to inhibit the nuclease activity of RecBC.
This experiment turned out to not be in my notebook because it was done by an undergraduate working in the lab. She did good work, but I can't find her lab notes on our shelf of old notebooks. (I hereby vow to work with our new lab assistant to get these notebooks better labeled and organized.) My notes of her lab meeting presentations and other discussions don't directly address this point.
But I gradually remembered that her initial results had been wrong (maybe that the strain she thought was a double dprA recBC mutant was actually only a single recBC mutant?), and that correcting the error had eliminated this interesting result, replacing it with a more solid but less interesting one. I did find a copy of her final report . It shows clearly that the double mutant had the same transformation phenotype as the single dprA mutant, so she concluded that DprA's job is not to inhibit the nuclease activity of RecBC.
What's species got to do with it?
Today I'm one of the speakers at a one-day symposium (sponsored by the Swedish government and organized by Patrick Keeling) in honour of the 300th birthday of Linnnaeus. The focus of the symposium is "Species", so I've been working to integrate issues surrounding species to my talk on "Do bacteria have sex?".The two pictures at the left illustrate how genetic exchange transforms what would otherwise be a clonal population into a species. Think of each skinny line as representing a gene or allele. In the clonal population, all the alleles in any one genome stay together (the broad green bars represent genomes). Alleles change only by rare mutation, so each allele becomes specialized to work well with only the particular alleles of other genes that are present in its own genome.
But in populations with sexual reproduction, all the alleles of the genomes' genes are reshuffled each generation. The two sets of alleles we inherited from our two parents are recombined into new single sets in the gametes we contribute to our children. That's why I've represented the sexual species by a mesh, like macrame, with different strands coming together and then separating to join with other strands. This frequent changing of 'genetic environment' means that individual alleles can't specialize, but must be generalists, able to work well with all the alleles of all the other genes in the population. This is what creates the genetic cohesion that makes a biological species.
A function for the appendix? (sloppy science, slick spin)
A paper proposing a function for the human appendix is all over the news. The paper itself is in Journal of Theoretical Biology (Articles in Press). I'd post a copy of the pdf but the journal is published by Elsevier and they'd probably put me in jail, so instead here's the Abstract
Other issues:
The human vermiform (“worm-like”) appendix is a 5 to 10 cm long and 0.5 to 1 cm wide pouch that extends from the cecum of the large bowel. The architecture of the human appendix is unique among mammals, and few mammals other than humans have an appendix at all. The function of the human appendix has long been a matter of debate, with the structure often considered to be a vestige of evolutionary development despite evidence to the contrary based on comparative primate anatomy. The appendix is thought to have some immune function based on its association with substantial lymphatic tissue, although the specific nature of that putative function is unknown. Based (a) on a recently acquired understanding of immune-mediated biofilm formation by commensal bacteria in the mammalian gut, (b) on biofilm distribution in the large bowel, (c) the association of lymphoid tissue with the appendix, (d) the potential for biofilms to protect and support colonization by commensal bacteria, and (e) on the architecture of the human bowel, we propose that the human appendix is well suited as a “safe house” for commensal bacteria, providing support for bacterial growth and potentially facilitating re-inoculation of the colon in the event that the contents of the intestinal tract are purged following exposure to a pathogen.Their points (a) to (e) are fine, but the conclusion depends on the totally unjustified assumption that a severe bout of diarrhoea eliminates commensal bacteria from the colon. Of course diarrhoea can reduce the number of bacteria in the colon, and cholera is likely to disrupt its epithelial biofilms. But even the most severe diarrhoeal infections are very unlikely to sterilize it, largely because there will be so many microenvironments within the colon that retain at least part of their biofilm. Biofilms are notoriously difficult to remove and to sterilize.
Other issues:
- What about animals that don't have an appendix? Only humans and anthropoid apes have appendices, but they are certainly not the only animals that get diarrhoeal infections. The authors argue that humans in Western cultures don't need their appendices because they're so rarely at risk of contracting the severe diarrhoeal diseases that the authors postulate necessitate reinoculation from the appendix. But animals are much more like humans in primitive cultures than like affluent humans.
- Some of the news reports (but not the paper itself) suggest that humans in primitive cultures need their appendix for reinoculation because populations are sparse and reinoculation from other people would not be reliable. But humans always live in social groups, and one thing severe diarrhoea does is spread intestinal bacteria around the environment, making reinoculation even more likely that it would otherwise be.
Mysterious old DprA data
I'm preparing a talk on "Do Bacteria Have Sex" for a symposium celebrating the 300th birthday of Linnaeus. While looking through old PowerPoint slides for ones appropriate for this topic and this audience and this amount of time, I found this slide, from a 2004 talk.I don't know whether I'd forgotten about this data because subsequent experiments proved it wrong, or just because I'm forgetful. I've written a couple of posts about the DprA protein (here and, more recently, here) - the main issue is that it protects DNA from degradation, but we don't know how or why.
I do remember doing these and related experiments; I just don't remember getting this very interesting result. The logic is as follows: The recBC genes specify a nuclease that degrades DNA. The degradation can facilitate recombination, which is how the nuclease was discovered and why the genes have 'rec' names, but its primary function is to help resolve stalled/tangled replication forks. If DprA's job is to protect DNA from the RecBC nuclease; then cells that lack the recBC gene shouldn't need DprA. The experiment shows that this is the case; the transformation frequency of the recBC dprA double mutant is much higher than that of the dprA single mutant, even though on its own the recBC mutation does decrease transformation slightly. In genetic terms, the recBC mutation is epistatic to the dprA mutation (it covers up the dprA phenotype).
Now I really need to go back to my 2003/04 lab notebook to find out exactly what I did and what I thought it meant.
Paper progress
Yesterday we sent the revised and we hope finalized version back to the journal editor. The requested revisions were minor and we did them all (the first-author post-doc did them all), so we expect the manuscript to be accepted.
And I posted the latest draft of the manuscript about uptake sequences in bacterial proteomes onto the Google site my collaborator had set up for file sharing. This site is a nice tool for collaboration. Before we were emailing versions of figures back and forth, so that when I needed a file I'd have to search for the appropriate version on my computer, (and later discover that I had the wrong version). But now the versions are all available in one place on this site, so I can easily tell which is the one I want. (Yes, I could have/should have just sorted the emailed files into the right folders when they arrived on my computer. I did try to do this but I still wound up with a mess.)
Today the post-docs and I meet to begin our discussion of the old H. influenzae transformation literature (papers pre-1970 this time). And I'll try to find time to check the concentrations of our new RNA preps and run them in a gel to check quality; the collaborating lab would like to have them by Tuesday.
And I posted the latest draft of the manuscript about uptake sequences in bacterial proteomes onto the Google site my collaborator had set up for file sharing. This site is a nice tool for collaboration. Before we were emailing versions of figures back and forth, so that when I needed a file I'd have to search for the appropriate version on my computer, (and later discover that I had the wrong version). But now the versions are all available in one place on this site, so I can easily tell which is the one I want. (Yes, I could have/should have just sorted the emailed files into the right folders when they arrived on my computer. I did try to do this but I still wound up with a mess.)
Today the post-docs and I meet to begin our discussion of the old H. influenzae transformation literature (papers pre-1970 this time). And I'll try to find time to check the concentrations of our new RNA preps and run them in a gel to check quality; the collaborating lab would like to have them by Tuesday.
A simpler test for transferred genes?
What if we just plotted base composition as a function of USS or DUS number (really the number of perfect matches to the USS or DUS core). If some genes lack uptake sequences because they've only recently entered the genome (coming from a source genome with no uptake sequences), we predict that genes with aberrant base compositions will be preferentially found in the class with no uptake sequences.
I imagine a graph looking something like this. Each dot represents a gene. Almost all the genes have base compositions close to 38%; this gives far too many points to resolve so the number of points in this group is indicated by the pale blue circles. I could clarify this by writing the actual numbers in blue beside these circles.
The numbers below the 0, 1, etc. on the bottom axis would be the fraction of the genes in that group that had aberrant base compositions. If our hypothesis is correct that newly acquired genes tend to lack uptake sequences, I anticipate these fractions would be highest for genes with no uptake sequences.
Doing this analysis would be much simpler than one that incorporated BLAST search results. On the other hand, the BLAST searches are already done, so maybe we can do both. But probably we should do this first, just to see if there is support for our hypothesis. If there isn't we'll know not to waste time doing the fancier analyses. If there is, we should also do this using codon adaptation index instead of base composition. I found a web page that calculates this index, but only one gene at a time, and I think my collaborators could probably automate it quite easily. (Maybe codon adaptation index has been replaced by a better measure - I'd better do some searching.)
I imagine a graph looking something like this. Each dot represents a gene. Almost all the genes have base compositions close to 38%; this gives far too many points to resolve so the number of points in this group is indicated by the pale blue circles. I could clarify this by writing the actual numbers in blue beside these circles.
The numbers below the 0, 1, etc. on the bottom axis would be the fraction of the genes in that group that had aberrant base compositions. If our hypothesis is correct that newly acquired genes tend to lack uptake sequences, I anticipate these fractions would be highest for genes with no uptake sequences.
Doing this analysis would be much simpler than one that incorporated BLAST search results. On the other hand, the BLAST searches are already done, so maybe we can do both. But probably we should do this first, just to see if there is support for our hypothesis. If there isn't we'll know not to waste time doing the fancier analyses. If there is, we should also do this using codon adaptation index instead of base composition. I found a web page that calculates this index, but only one gene at a time, and I think my collaborators could probably automate it quite easily. (Maybe codon adaptation index has been replaced by a better measure - I'd better do some searching.)
no homolog or weak homolog?
With my Ottawa bioinformatics colleagues I'm analyzing the effects of uptake sequence accumulation on the H. influenzae and N. meningitidis proteomes. One issue I'm struggling with right now is how to tell the difference between genes that give poor "E-value" scores in BLAST searches against test genomes from the same group (e.g. gamma proteobacteria) because they have no true homologs in the test genomes being searched, and genes that give poor scores because they have no homologs in these genomes. The latter genes would be ones that were acquired by transfer from more distantly-related bacteria. I know (at least in principle) how to use phylogenetic analysis to show that a gene has been acquired by lateral gene transfer (LGT) rather than having simply diverged, but here I'm looking for a less rigorous and more automatable method, one that can be used to quickly screen many genes (say 100).
So far I think we could use a combination of low BLAST score against the test genomes and aberrant base composition and codon adaptation index to identify genes that are good candidates for having been acquired by LGT. But I'd like to go one step further - to do one more test where genes acquired by LGT are predicted to differ from genes that have simply diverged in situ.
One test I'm considering would be to take the genes that the base composition and low CAI tests flagged, and BLAST them against a closer relative (something in the same family). If the genes are just divergent, they should give higher scores with the relative. But if they were acquired by LGT, they should either give very high scores (if they were acquired before the H. influenzae and relative lineages diverged) or just as low scores (if they were acquired by the H. influenzae lineage after the relative diverged. The analysis should be also done on a control set of genes, ones that had equally low BLAST scores in the original tests but normal base composition (38% G+C) and codon adaptation indices (???). The BLAST scores of these genes should be modestly higher against the close relative than against the test genomes.
So. Prediction: Control gene set, blasted against close relative: most (all?) BLAST scores modestly higher than with test genomes. LGT gene set, blasted against close relative: Some BLAST scores much higher than with test genomes, others not improved at all.
So far I think we could use a combination of low BLAST score against the test genomes and aberrant base composition and codon adaptation index to identify genes that are good candidates for having been acquired by LGT. But I'd like to go one step further - to do one more test where genes acquired by LGT are predicted to differ from genes that have simply diverged in situ.
One test I'm considering would be to take the genes that the base composition and low CAI tests flagged, and BLAST them against a closer relative (something in the same family). If the genes are just divergent, they should give higher scores with the relative. But if they were acquired by LGT, they should either give very high scores (if they were acquired before the H. influenzae and relative lineages diverged) or just as low scores (if they were acquired by the H. influenzae lineage after the relative diverged. The analysis should be also done on a control set of genes, ones that had equally low BLAST scores in the original tests but normal base composition (38% G+C) and codon adaptation indices (???). The BLAST scores of these genes should be modestly higher against the close relative than against the test genomes.
So. Prediction: Control gene set, blasted against close relative: most (all?) BLAST scores modestly higher than with test genomes. LGT gene set, blasted against close relative: Some BLAST scores much higher than with test genomes, others not improved at all.
Growing cells and making RNA (continued)
On Thursday and Friday I finally was able to collect cells from cultures of wildtype H. influenzae cells growing happily (exponentially) in medium with and without a sub-inhibitory concentration of rifampcin. On Friday I did a RNA prep of the cells I'd collected on Thursday, working with our new undergraduate assistant. Yesterday the undergrad did the RNA preps of Friday's cells by herself.
And tomorrow, she and I will run a gel to check that the RNAs are in good shape (not degraded), treat them with DNA-Free, and pass them on to our collaborators for real-time PCR analysis.
And tomorrow, she and I will run a gel to check that the RNAs are in good shape (not degraded), treat them with DNA-Free, and pass them on to our collaborators for real-time PCR analysis.
Salmonella in space
A paper I've been waiting to see finally appeared, several days after the news articles about its findings. (Larry Moran has a post today about PNAs's wicked practice of letting the media gush about results of papers that aren't yet available.)
Here's what the news reports said:
This left me thinking that the genotypes of the bacteria had consistently mutated (cosmic rays) in a way that made them more virulent. From an evolutionary perspective this seemed very improbable - both in having similar mutations arise in many bacteria and in having the bacteria direct their mutations to fit their changed environment.
Now I read the paper I discover that the genes hadn't changed at all. As the title indicates, what had changed was the expression of some genes (some turned up and some down) - this is a transient response to the altered culture conditions in space, not a genetic change. The cells in the culture that had been in space were more clumped together, in what may be the zero-gravity broth-phase equivalent of a biofilm. These bacteria caused more serious disease when injected into mice, probably because the clumping made it harder for the mouse immune system to kill them.
Space flight alters bacterial gene expression and virulence and reveals a role for global regulator Hfq. J. W. Wilson et al. (many authors), PNAS Sept. 27 2007. Link
Here's what the news reports said:"The researchers found 167 genes had changed in the salmonella that went to space..."
Dr. Cheryl Nickerson, the PI on the project, is quoted (misquoted?) as saying "These bugs can sense where they are by changes in their environment. The minute they sense a different environment, they change their genetic machinery so they can survive."
This left me thinking that the genotypes of the bacteria had consistently mutated (cosmic rays) in a way that made them more virulent. From an evolutionary perspective this seemed very improbable - both in having similar mutations arise in many bacteria and in having the bacteria direct their mutations to fit their changed environment.
Now I read the paper I discover that the genes hadn't changed at all. As the title indicates, what had changed was the expression of some genes (some turned up and some down) - this is a transient response to the altered culture conditions in space, not a genetic change. The cells in the culture that had been in space were more clumped together, in what may be the zero-gravity broth-phase equivalent of a biofilm. These bacteria caused more serious disease when injected into mice, probably because the clumping made it harder for the mouse immune system to kill them.