Examples of good astrobiology please

The comments on my short post about whether my original criticism of the Wolfe-Simon paper was too 'personal' bring up the issue of whether 'astrobiology' is a genuine research field, or just a catchy title applied to conventional biology funded by NASA's astrobiology program.  Because the only papers from this program that come to my mind are seriously flawed*,  I want to raise a related question - what good science has this program produced? 

I know of excellent biologists funded by NASA, so I'm sure there are good papers out there.  I guess I'm wondering whether there's an inverse relationship between a paper's quality and its claims of astrobiological relevance.

Here are the bad papers I'm thinking of:

1.  The Mars meteorite paper (1996):  Here's a more even-handed evaluation than I would give it.

2.  This nanobacteria paper (2005):  I haven't posted about it, but the structures called 'nanobacteria' appear to be just aggregations of calcium salts.  I don't think any reputable microbiologist believes that they are bacteria.  Here's a critical review from PNAS.

3.  The Salmonella in microgravity paper (2007): See this post for my evaluation.

4.  The arsenic-DNA paper (2010): See this post for my evaluation.

5.  The fossil bacteria in a meteorite paper (2011): See this post for my evaluation.

So, commentors, please point me to good astrobiology papers. 

Just to clarify (after reading the comments so far):  What I'm looking for is papers that report competent experimental research and that self-identify as 'astrobiology'.


* Yes, I know that my memory of astrobiology papers is no doubt flawed because only the bad ones stick in my mind.  That's why I'm asking.

Phage recombination: testing the postdoc's idea

I'm all set to do the phage recombination assays I described earlier here and here.  But the postdoc has a clever hypothesis that I hadn't thought of, that can be easily tested.

I set up our new/old incubators at 33°C and 41°C, and used them to assay the titers (plaque-forming units per ml; pfu/ml) of the phage lysates I made a couple of weeks ago.  These temperatures turned out to be just right (this is a Goldilocks assay); the 41°C incubator wasn't too hot for the cells to grow and the 33°C incubator wasn't too cool for plaques to form.  My lysates of the three temperature-sensitive mutant phages all had titers of 5-8 x 10^10 pfu/ml at 33°C and titers of less than 10^6 at 41°C.  These high titers  mean that it will be easy to set up mixed infections where most cells are infected by phage of two different genotypes, and the low background means I can sensitively detect recombinants.

My original plan was to screen all of our competence-gene knockout strains for the ability to promote phage recombination.  This recombination has long been known to occur much more efficiently in competent cells and to not occur in the few competence mutants where it has been tested (crp, cya, sxy and rec2), so I've hypothesized that the ability to recombine phage DNA reflects a competence-induced change in DNA metabolism.  This means that I can use phage recombination as a probe for the competence-induced changes in DNA metabolism.

BUT, this hypothesis fails to explain why phage recombination isn't induced by competence in the rec2 mutant.  The defective Rec2 protein in rec2 mutants is thought to only block transfer of DNA from the periplasm to the cytoplasm.  We know that competence-induced DNA uptake across the outer membrane is unaffected, and we expect that competence-induced cytoplasmic changes also occur normally.  So why wouldn't phage recombination happen in these cells?

I had already considered one explanation.  Phage recombination is known to need the Rec1 (RecA) pathway of homologous recombination.  This pathway may be enhanced in competent cells, but not because the rec1 gene is part of the competence regulon.  Rather, we think the Rec1 protein, like its RecA homolog in E. coli, is activated by the single stranded DNA that competent cells bring into the cytoplasm.  DNA isn't deliberately added to cultures being tested for phage recombination, but I hypothesized that that normal cultures of competent cells might contain significant amounts of free DNA from cells that died during incubation in the starvation medium, and that uptake of this DNA might activate Rec1 recombination.  I think I might even have done a test of this years ago, by adding DNase I to the starvation medium, but if so the results were inconclusive.

The postdoc has a better idea.  He reminded me that phage lysates typically contain significant amounts of free phage DNA (DNA that had not been packaged into phage capsids before the cell lysed), and that competent cells can take up this DNA.  So maybe the recombinant phage are produced not by recombination between the DNAs of two independently infecting phages replicating in the cytoplasm of a single cell, but by recombination between the DNA of a single infecting phage and DNA of a different phage that has been brought in by the competence machinery!

I don't know how much free phage DNA a lysate would contain, but I bet it's at least as much as the amount of DNA packaged in the phage particles.  In recombination assays cells are typically incubated with both phages at a 'multiplicity of infection' greater than 1 to ensure that most cells are infected by both phages (that's why I need high-titer lysates), so these incubations also provide the cells with lots of free phage DNA that they may take up by the competence pathway.  And we know that phage DNA is taken up efficiently because it contains lots of uptake sequence.

The easiest test of the postdoc's hypothesis is to incubate the mutant phage lysates with DNase I before mixing them with the cells.  If he's right this should dramatically reduce phage recombination without affecting phage replication.  This doesn't really distinguish between his hypothesis and mine, so a better test would be to purify DNA from the lysates and test recombination in infections where cells are incubated with a lysate of one mutant phage and DNA from a different mutant.  I calculate that my lysates contain about 4 µg/ml of phage DNA in virions, so a simple DNA prep from a few ml should give me enough DNA for this test.  Another test would be to precipitate out the intact phage from a lysate (I think this is easily done using polyethylene glycol (PEG)) and show that its titer is way down but its contribution to recombination is not. 


I had thought of phage recombination as providing a way to probe the state of DNA metabolism, one independent of the usual assays of chromosomal transformation.  But if phage recombination turns out to occur by uptake dependent recombination of  translocated phage DNA (single-stranded) with replicating phage DNA, then it's just another transformation assay, differing only in the target being phage DNA rather than chromosomal DNA.  It still might be a useful probe, but not in the way I was thinking.

Were my original #arseniclife criticisms overly personal?

The PaleBlue astrobiology blog has a new post titled High Impact Science in a Hyperactive Media Environment, discussing lessons to be learned about how to discuss adaptations that are needed to effectively communicate high-profile science in the current media environment.

In general I agree with the points being made.  But I take disagree with how a quote from my original post about the Wolfe-Simon paper is described under Lesson 2: Blogs are a public microphone, and people are listening.  Here's what I wrote:

"I don’t know whether the authors are just bad scientists or whether they’re unscrupulously pushing NASA’s ‘There’s life in outer space!’ agenda.  I hesitate to blame the reviewers, as their objections are likely to have been overruled by Science’s editors in their eagerness to score such a high-impact publication."

The author of the blog then says:

This paragraph is both inaccurate and unfounded. The author of this blog post (Dr. Rosie Redfield) followed a detailed technical critique with a slate of personal attacks, snark, and assumptions as to the motivations of the authors, NASA, and Science’s editors.

I've seen complaints about these two sentences elsewhere, most recently here, and I don't think they're valid.  Here's the comment I just posted on the PaleBlue blog:

Despite all the opprobrium attracted by those two sentences in my original post, I still think they nicely distribute the responsibility for what everyone agrees was a truly terrible paper.

Producing some bad science does not automatically make one a bad scientist, but the authors' continuing refusal to admit they made any mistakes is not a good sign.  NASA's financial support for the work certainly played a role, as probably did the publicity they eagerly provided.  I doubt that the paper would have been accepted if all the reviewers had identified the obvious errors, and Science's editors were certainly complicit in the decision to publish.

How might a bacterium evolve to use arsenic in place of phosphorus?

Implicit in the Wolfe-Simon paper on arsenic-using bacteria is the assumption that evolving in a high-arsenic environment has caused the GFAJ-1 bacteria to increase their fitness by becoming able to use arsenic in place of phosphorus.  There are some problems with this that I think have been overlooked.

The issues are so interconnected that I'm having a hard time pulling them apart to explain them*.  One issue is the descent of GFAJ-1 from ancestors that used phosphorus and not arsenic for metabolism and for nucleic acids.  Another is the numbers of genes and proteins that would have to be different if a cell used arsenic in place of phosphorus.  Another is the selective advantage of using arsenic in an environment with abundant arsenic and little phosphorus**.  In my attempt to explain these I'm going to ignore the metabolically devastating instability of arsenic-ester bonds.

All known organisms need phosphorus to make DNA, RNA, ATP and NADP, and many metabolic reactions either require addition of phosphate groups to small molecules or act on molecules with attached phosphates.  Phosphorylation also regulates the activity of many proteins.  Thus a cell that used the same basic metabolic pathways but with arsenic rather than phosphorus would need to have arsenic-specific versions of all proteins that interact with any of these molecules.  Because phosphorylation is so ubiquitous, this is likely to be at least half of the proteins in the cell.  This means that full replacement of phosphorus with arsenic could not have arisen in a single step, because replacement requires changing so many different genes.

How could it have arisen?  Because GFAJ-1 is a member of the known biosphere, we need to start with an ancestor that had conventional phosphorus-based metabolism. Because just about all cellular phosphate enters the system by way of ATP (if I remember my biochemistry correctly), the simplest way (perhaps the only way) to begin using arsenic would be a mutation in an enzyme that attaches free phosphate to a metabolite.  I'm thinking of an ATP synthase that normally puts inorganic phosphate onto ADP to make ATP.  But this hypothetical arseno-version of ATP would only be useful if other proteins could use it.  Initially it's more likely to be toxic to all the normal proteins that interact with ATP and with phosphorylated metabolites.  The number of mutations required to adapt this many proteins to tolerating arsenylated versions of their substrates would be prohibitive.

We can separately consider the magnitude of the selective benefit that would be achieved by replacing phosphorus with arsenic.  In an arsenic-rich phosphorus-limited environment, complete replacement of P with As would give a large competitive advantage (all else being equal).  However, an organism that replaced only a small fraction of its phosphorus with arsenic (as is now claimed for GFAJ-1) would obtain only a proportionately small growth advantage over cells entirely dependent on phosphorus.  For example a cell that replaced 1% of its P with As would still need 99% as much P as its competitors.  A bacterium could achieve the same advantage much more easily by a 1% improvement in the affinity of its phosphate uptake system.

A 1% selective advantage certainly isn't trivial, and, all else being equal, a mutation causing this advantage would be expected to take over a population.  But all else isn't equal if the advantage comes from substituting arsenic for phosphorus.  Rather, replacing a small fraction of the cellular phosphorus with arsenic creates even bigger problems than replacing all of it.  That's because the proteins would have to be able to use both phosphorylated and arsenylated substrates

I think the paper's authors may have been led astray by their initial hope that GFAJ-1 was a member of a shadow biosphere that used only arsenic (not phosphorus) for all of the cellular processes that members of the known biosphere use phosphorus for.  Such a cell would have an integrated arsenic-based metabolism and, if we set aside the chemical stability problems, its recent evolution would be no more problematic than that of phosphorus-based bacteria.  However, once GFAJ-1 was discovered to be a member of the known phosphorus-based biosphere, the authors may not ahve rethought how it could have evolved to have the arsenic-using properties they are attributing to it.

* I suspect the difficulty I'm having in clearly explaining the problems isn't a writing problem.  Instead, it's caused by the many intrinsic contradictions that arise when we consider how GFAJ-1 might have evolved to use arsenic.

**  Mono Lake, the natural environment of GFAJ-1, has abundant phosphorus (400 µM) and arsenic (200 µM).

How to test the arsenic-DNA claims

I've been saying that researchers shouldn't invest the time and resources needed to test Wolfe-Simon et al's claims, because of the vanishingly small probability that they are correct.  But I'm having second thoughts, because the most important claims can, I think, be very easily tested.  So I've just sent an email off to GFAJ1samplerequest@gmail.com (thanks Dave Baltrus, @surt_lab, for tweeting this address), asking for information on how to obtain the bacterial strain GFAJ-1.

The main questions to answer are:

Q. 1.  Is the approximately tenfold growth difference between +As/-P and -As/-P in Figure 1B due to the cells' use of As in place of P in DNA, RNA and other biomolecules?

Q. 2.  Does DNA purified from cells grown with limiting P and abundant As contain significant amounts of covalently incorporated As?

Both of these questions can be answered by straightforward experiments.  However a microbiologist like myself would need to work with someone (a chemist?) who could use a mass spec to assay As and P in the reagents, media and DNA.  I'm assuming this is very straightforward, but perhaps readers can set me straight if I'm wrong.

I'll consider Q. 2 first because it initially seemed easiest.  

1.  Make culture media with 40 mM arsenate and varying levels of phosphate (at least 0, 3 and 1500 µM).  The recipe for the base of 'AML60 salts' is available here; unfortunately this reference does not give the components of the 'trace metals stock' it uses, nor does the reference it cites.  Don't worry about any phosphate contamination of the medium.

2.  Inoculate the GFAJ-1 cells into the different media and culture them in screw-top vials at 28 °C in the dark.  The Methods don't say anything about mixing, so probably stationary culture with occasional mixing is OK.  I could turn down the temperature of one of my new/old incubators if we were to do this.

3.  Monitor the culture growth by counting a defined volume of the cells under a microscope (a hemocytometer is useful for this).  The cells will probably double every day or so. 

4.  Once the cells have stopped dividing, collect them by centrifugation and wash them several times with a simple solution such as PBS.

5.  As a control for arsenic contamination, add to arsenic medium an equal number of E. coli cells that have been grown in medium without arsenic, and let them sit for a couple of hours.  Then collect them and wash them along with the GFAJ-1 cells.

6.  Mix the cells with 50 mM Tris 10 mM EDTA (no more than 10^9 cells per ml) and lyse them by adding SDS to 1%.  Add RNase A (10 mM) and incubate at 37 °C for 20 minutes to degrade the RNA.  Extract the lysed cells with twice with phenol and twice with phenol:chloroform.  

7.  To the aqueous phase add NaCl (150 mM) and ethanol to 70%.  Collect the chromosomal DNA by spooling it onto the sealed tip of a glass Pasteur pipette.  Wash the DNA by rinsing the tip with 70% ethanol, and let the DNA air-dry on the tip.

8.  Dissolve the DNA in TE (10 mM tris 1 mM EDTA), aiming for a concentration of about 200 µg/ml, based on the number of cells you had in each prep. 

 Now further purify each DNA using all three of the following methods.  Each method has different advantages and is likely to remove different kinds of contaminants, and I've ordered them by the amounts of DNA they can handle.  (Perhaps you should first ask your chemist how much DNA is needed for mass spec analysis.):

9.  Repeat the spooling precipitation:  Add NaCl and ethanol, and again spool the DNA as it is driven out of solution by the ethanol.  Spooling works well with chromosomal DNA because the DNA concentration is usually high and the DNA fragments are long.  It is preferable to centrifugation because small ethanol-insoluble molecules that would pellet with the DNA are left behind.

10:  Purify the DNA on a spin column:  These columns will bind about 10 µg of DNA, and the bound DNA can then be washed by repeatedly passing an alcohol solution through the column.  The DNA is then eluted by washing TE through the column.

11. Purify the DNA by gel electrophoresis:  Load some of the DNA into the well of an agarose gel, and electrophorese it until the DNA has migrated several cm into the gel.  Use a small enough amount of DNA and a large enough gel and well that the DNA runs as a clean band and not as a smear.  Cut out the band and purify the DNA away from the agarose and gel buffer using a spin-column kit.

12.  Give the DNAs to the chemist for mass spec analysis.  Be sure to have DNA from bacteria other than GFAJ-1, grown without arsenic, with and without soaking the cells in arsenic medium before DNA purification.

This may sound like a lot of work, but steps 4 - 12 can easily be completed for 3-6 DNAs in a single day.  If the DNA from cells grown in As plus limiting P contains no more arsenic than the other DNAs, then the answer to Q. 2 is "No".

Now I'll consider Q. 1.  It's just like the first steps of Q. 2, but with the mass spec done on the media at the beginning rather than on the DNA at the end.


1.  Find out how much phosphate contamination to expect in ultra-pure versions of the reagents needed to make the AML60-based culture media - your chemist collaborator should have access to this information.  Use this information to calculate how much P to expect in the basic medium with and without As.  You could skip this step, but it would be prudent to check this in advance.

2.  Order ultra-pure reagents and make the media, or have your chemist collaborator make the media.  You want each of the following:  plain glucose media with no added As or P, media with 3 µM P and no As, media with 40 mM As and no P,  media with 3 µM P and 40 mM As, and media with 1500 µM P and 40 mM As.

3.  Have the chemist assay the media for As and P by mass spec. 

4.   Inoculate the GFAJ-1 cells, first washing them to remove traces of whatever medium they've been growing in/on.

5.  Monitor the culture growth by counting the cells under a microscope.  The cells in cultures with added P will probably double every day or so.


6.  Once the cells have stopped dividing, plot cell numbers as a function of time for each medium.  If final cell density is proportional to the amount of P in the medium, then the answer to Q. 1 is "No".

Maybe have the chemist assay the spent media from the low-P cultures to see how the P concentration has changed.

Of course, for either experiment the most important practical question is 'Could these results be published?'  I think they could.  The best plan would be to have several independent labs do the same test and publish jointly - we'd have more impact and all get our names on a publication.  On the other hand, we all have more important things to do...

Wolfe-Simon et al.'s responses to my comments

This is the first of three more #arseniclife blog posts; the others will consider possible experimental tests of the claims and some evolutionary issues that have been overlooked.

The brief Letter to Science that I composed here (with help from some readers) was one of the eight published today.  The Letter was converted to a 'Technical Comment' by the Science Editorial Office, I guess because it contained technical comments, and had one-paragraph peer reviews from 5 (!) reviewers.  I think Science must have sent all the submissions to the same group of reviewers, who gave each a very brief review.

The Letter made three main points, and I'll treat the authors' responses to each in turn:

1. Because one or more of the reagents used for the culture media were contaminated with phosphate, the growth attributed to arsenic is better explained by growth on phosphorus.  I and several other commenters pointed out that the 3 µM PO4 contaminating most of the media they analyzed would be sufficient to fully explain the observed increase in number of cells.  (My calculation is explained at the end of this post.)

The authors disagree, pointing out that the cells contained less phosphate per total dry weight than needed for growth.  But their dry weight measurements were inflated by the high content of the storage hydrocarbon polyhydroxybutyrate, which contains no phosphate, so this analysis is not valid.

The authors also point out that the cells grew on medium supplemented with As (+As/-P) but not on medium supplemented with neither As nor P.  The graph below is their Fig. 1B, and it shows that the +As/-P culture reached a tenfold higher cell density than the -As/-P  culture.  They say that both media contained the same  ~3 µM PO4 contamination, so the difference in growth must be due to use of As in place of P.  If that were indeed the case, we would expect the cells' DNA and RNA to consist of about 90% As bonds and 10% P bonds, which is certainly not supported by the elemental analyses.

Two other explanations are much more likely.  First, because the bacteria have evolved in an arsenic-rich lake, they might be dependent on arsenic for some metabolic process.  However the cells grew fine in medium with added phosphate.  A perhaps more likely explanation is that the medium used for the -As/-P control did not contain the same level of phosphate contamination.  The data beside the graph in the above figure shows the reported phosphate contamination of different batches of media and solutions.  One batch of medium had no detectable P contamination (< 0.3 µM), despite the authors 'assertion that all media were made up from a stock containing 3 µM P.  This implies that either the media was variably contaminated or the P measurements were unreliable.  The paper does not indicate which batch of medium was used for any given experiment, and the actual source(s) of the P contamination have not been identified (or even sought). 

2. The DNA was not properly purified before gel electrophoresis.  The Methods stated that after extraction with phenol and phenol:chloroform the DNA and RNA was precipitated with ethanol and the pellet resuspended in sterile water.  I pointed out that such organic extractions do not remove any substances such as simple salts that are more soluble in water than in phenol or phenol:chloroform, and that such substances are often less soluble in 70% ethanol and thus would contaminate the pellet.

The new response repeats the authors' earlier claim that phenol and phenol:chloroform extractions remove arsenate and other 'impurities' from the aqueous phase; they provide no citation or experimental evidence to support this statement.  These extractions remove lipids into the organic phase and denature proteins, which form insoluble aggregates at the interface, but I know of no evidence that they remove small hydrophilic molecules such as arsenate.  I've asked other molecular biologists about this and they agree.

The response now says that the pellet from the ethanol precipitation was washed with 70% ethanol before being dried and resuspended in water for further analysis.  This will have removed contaminants that had remained dissolved in the alcohol supernatant, but may not have removed any insoluble material that was pelleted with the nucleic acids.

3.  The DNA was not purified away from the agarose gel before elemental analysis.  After the ethanol-precipitated DNA was resuspended in water it was run in an agarose gel.  Gel electrophoresis is one of the standard ways of obtaining highly purified DNA; it works partly because most contaminants have different electrophoretic mobilities in agarose than DNA does.   But it's essential to then separate the DNA from the agarose that surrounds it.  The authors didn't do this, although it's a standard lab procedure that can be done in 10 minutes with a simple column kit stocked by most labs.  Instead they analyzed the DNA together with the agarose slice it was embedded in.  Because the gel slice contained only about 1 µg of DNA and about 100 mg of 1% agarose gel, it would have contained about 1000-fold more agarose than DNA and about 300-fold more buffer salts than DNA.  Any contaminants in the agarose or in the buffer, or any contaminants introduced with the DNA, would thus have shown up in the elemental analysis.

The authors provide no explanation for leaving the DNA in the agarose.   Instead they just say "Analysis of DNA separated from agarose would be a useful future experiment...".  They follow this with a brief discussion of how their control for the DNA-in-gel analysis may not have been very good, but without in any way admitting that their analysis was flawed.

- - - - - - - - - - - - - - - - - - - - - - - - - - - - - - - - - -

Overall, the most striking aspect of the authors' formal response is that they never admit to having made any mistakes or having done anything badly.  This is a bit disconcerting, given how many concerns were raised.

Arseniclife: The formal critiques and the authors' responses

Last December Wolfe-Simon and 11 coauthors published a paper claiming to show that bacteria isolated from an arsenic-contaminated lake could not only grow in the presence of very high concentrations of arsenic but could incorporate arsenic into their DNA in place of phosphorus.  The paper was harshly criticized for its lack of controls and unjustified conclusions.

The paper has been available only as a pre-publication preprint on the Science Express site, where it has languished for the past 6 months.  But today Science finally provides pre-publication copies of 8 Technical Comments on the paper, along with a formal response from the authors.  The original paper, the comments and the response will all appear in the print edition of Science next week (June 3 issue).

The authors don't report any new experiments.  Most of their responses take the form of 'our interpretation could be correct on this point if...'.  In many cases there is indeed a small possibility that it could, but there are so many of these points of interpretation, each with only a very small probability of being correct, that I don't think anyone will find the arguments convincing.

The authors are also finally making the bacteria available so others can test them.  It should be simple to find out whether arsenic is covalently incorporates into the DNA of bacteria grown with abundant arsenic but limiting phosphorus.  The microbiology and molecular biology are trivial, but you'd need a chemistry collaborator to do the phosphorus and arsenic assays.  (Probably a chemist would say that the chemistry is trivial but you'd need a microbiology collaborator to grow the cells and purify the DNA.)

Their responses to my Technical Comment are in some ways the most scientifically valid, as they provide information about their media and DNA purification.  I'll consider these in a separate post later today.

How best to screen for loss of competence

The RA and I are working on a better method to isolate cells carrying 'unmarked' knockouts of the genes in the CRP-S regulon.  She's made many mutations whose deletions are marked by addition of a SpcR StrS cassette.  In principle these cassettes should be easily removable by (i) induction of a plasmid encoding an 'excisionase' of some sort that removes the cassette (details not important here) followed by (ii) selection for the resistance to streptomycin created by removal of the dominant StrS allele.  But the plasmid is quite toxic and the selection doesn't work in our strain.  We really want the unmarked mutations because many of the CRP-S genes are in operons where marked mutations in 'upstream' genes are likely to interfere with expression of genes downstream in their operon (to be 'polar' on them).

One possibility would be to make the marked mutation in the other strain (where the StrR selection works), and then transfer it by transformation into our strain.  But we'd still have to screen our cells for the mutation, as there's no way to select for it.

The strategy we're testing now is to remove the cassette from the cloned marked mutations in E.coli, where everything works well, and to transform our strain with the unmarked fragment (from the plasmid or as a PCR product) and then screen the transformants for the expected phenotype (loss of transformation) or genotype (diagnostic PCR fragment).  If the transformation occurs at a sufficiently high frequency we'll be set.

So we're doing a test.  The RA amplified up two fragments, marked and unmarked versions of a rec-2 deletion mutation.  I've transformed these into wildtype cells and will now screen these for loss of transformation; because she's already made the corresponding H. influenzae strains I already know that the mutants will not transform at all.  Because the transformation may be inefficient I also included a small amount of NovR chromosomal DNA in the transformations and selected for acquisition of novobiocin resistance.  I meant to also select the marked transformants for SpcR, but used 10-fold too little spectinomycin in my plates.  (I'm going to reselect the cells to check this and get some known mutants.)

The big question is how I will screen the transformant colonies for loss of rec-2 function.  The old way was to replica plate the colonies onto an sBHI agar plate that had been spread with antibiotic-resistance DNA, let the cells grow up overnight, and replica-plate the resulting colonies onto sBHI agar with the antibiotic.   But this is far from quantitative, and the replica plating velvets we have always make ugly smears.  A cleaner way, though more work, would be to pick the colonies into sBHI broth containing DNA (and cAMP?), and later spot the cells onto selective sBHI agar.

I think I should let the screening wait until tomorrow, and first do the Spc plating to find out what frequency of transformants I should expect.

The 'fraction competent' problem

The new graduate student is considering potential research projects, and he's keen to work on the long-standing puzzle of why all the cells in a 'competent' culture aren't equally competent.  I don't think this is something we should be focusing our efforts on now, so below I'll try to explain why.

First I need to describe the initial observation and what we now know about it.  I originally blogged about it 5 years ago; that post explains the assay and the usual result.  Briefly, we can asses the variation in transformability of cells in a culture by transforming them with two selectable markers on separate DNA fragments.  If all the cells are equally competent the frequency of double transformants should be simply the product of the frequencies of single transformants; for simplicity I'll call the double-transformant frequency the 'expected' frequency.  Usually we find that the frequency of double transformants is much higher than the expected frequency, and we conclude that some cells in the culture are much more transformable than others.  (If we had found that the frequency of double transformants was instead much  lower than the expected frequency, we would conclude that many cells could only take up one fragment of DNA.)

Refs from my old notebook:  Goodgal and Herriott 1961, J. Gen. Physiol. 44:1201;  Porter and Guild 1969, J. Bacteriol.  97:1033; Bremer et al 1984, J. Bacteriol. 157:868.

The relationship between the observed and expected frequencies of double transformants can be used to calculate the 'fraction competent' of the cells in a culture.  But this calculation requires the simplifying assuming that competence is an all-or-nothing state.  If instead there's a gradient of competence, or if one subset of the cells takes up ten times more DNA than the rest, then the calculation doesn't apply.

That said, what we and others have found is that, whenever a culture has a high enough transformation frequency that the frequency of double transformants can be measured, the double-transformation frequency indicates that most of the transformation is being done by a subset of cells that are just as transformable as the transformable cells in a fully-induced culture.  This is true for all cultures with intermediate transformation frequencies (late-log growth, induction in log-phase with cAMP, partial competence of the sxy-1 mutant in log phase).

Here's what we've learned from these experiments:  Wildtype cells in log-phase growth give no transformants.  Cells at the end of log phase ('late-log) have a transformation frequency about 100-fold less than that of MIV-induced 'competent' cultures (~10^-4 vs ~10^-2), and the 'fraction competent' is about 0.5-1%  In MIV-induced cultures the 'fraction competent' is about 50% (well, 10%-50%; it partly depends on which markers are tested).  Adding cAMP to log-phase cells raises competence to the late-log level, with a 'fraction competent' of about 1%.

We've also examined double-transformant frequencies in the hypercompetent sxy1 mutant.  These cells are as competent in log-phase growth as Rd is in late log, and their 'fraction competent' is similar (0.5%) They are as competent in late-log as Rd is in MIV, and again the 'fraction competent' is similar (10-90%).  Competence in MIV is like that of RD, and the 'fraction competent' is similar too.

I mustn't forget that the 'fraction competent' measure is probably an oversimplification - the double-transformant analysis can't detect more subtle variations.  Here's a figure to make that point.

So, why don't I think this is a problem we should be actively working on?

I.  The most likely explanation is the least interesting:  The proximate causes are probably the combined effects of (1) the details of interactions between regulatory sequences and regulatory proteins, (2) random fluctuations in the cellular levels of regulatory proteins and metabolites and (3) differences in the cell-cycle stages of different cells (replicating DNA, dividing etc.).

II.  Investigating these factors would be very difficult.

III.  The phenomenon may be irrelevant to understanding why cells take up DNA:  The distribution of competence we see in lab cultures may well be an artefact of the culture conditions we use.  Understanding it is unlikely to help us understand how competence is controlled in the human host.

IV.  There may not be an ultimate cause at all - the proximate factors may not have been under direct selection.  On the other hand, if they have been shaped by selection to optimize the distribution of competence in the cell population (the subject of some just-so-story speculation), the nature of this selection will be very hard to characterize.

Progress at the bench

1.  I made lysates of all four phages.  Making lysates of HP1 phage is an act of faith, because inducing the prophage doesn't cause most of the cells in the culture to lyse.  When prophage lambda is induced in a lysogenic E. coli culture, the culture density increased for an hour or so and then the cells all lyse (the culture goes clear, with bits of threadlike cell debris visible).  But the induced HP1 lysogens just continue to get more dense, and never really appear lysed (though sometimes some debris is visible).

I've only titered the wildtype lysate because the 34°C and 41°C incubators can't be moved to our lab until next week.  Despite the lack of obvious lysis, the lysate contains about 5 x 10^10 plaque-forming units per ml, which is just fine.  If the temperature-sensitive mutants behaved similarly I'll have lots of phage for my recombination assays (the titer of the phage needs to be about ten times that of the cells, to get the necessary multiplicity of infection). 

2.  I've finished transformation assays on three of our new competence-gene knockouts.  Two of the genes, comA and comC are in the big comABCDEF operon; both mutations are 'unmarked' deletions and not expected to interfere with expression of the downstream genes in the operon.  The RA tells me that all of the genes in the homologous Neisseria meningitidis operon (pilMNOPQ) are needed for functioning of the pilQ-encoded secretin pore through which DNA is taken up (I haven't looked at the paper(s) yet), so we expect knockouts of these genes to completely eliminate transformation.  However, although the comC knockout did give no transformants at all, the comA knockout had a normal (wildtype) transformation frequency.  I think this probably isn't just a mistake on my part (e.g. a strain mixup), because the undergrad who worked on these mutants also saw high transformation frequencies for both the marked and unmarked comA mutants.  But we'll need to use PCR to confirm that the cells I'm using do have the right deletion.

I made six more mutants competent yesterday.  I'll analyze the results today, once the colonies get big enough to count.  And I'll streak out more mutants to transform tomorrow (I'm on a roll).

I also froze 3 ml of competent cells from each prep, to use in the phage-recombination assays.  These cells will also be used for the PCR-checking of genotypes.  The RA will do this - I need to ask her about how much preparative work is needed - can she just use the frozen cells directly in PCR or do we need to do DNA preps first?

Assay for phage recombination

I think I now have everything I need to assay the ability of phage to recombine in different H. influenzae competence mutants (the mitomycin C arrived yesterday), so I've gone back and looked at the procedure I used.  (Yes, I should have done this sooner...)  The procedure is a bit more complicated than I had remembered, but maybe I can streamline it.


The procedure (from my old lab notebook):

Need: 

1. Lysates of two phage strains carrying temperature-sensitive mutations in different genes (at least 10^10 phage/ml).
2. Culture of the bacteria to be tested (at least 10^9 cells/ml), in culture or competence medium.
3. Culture of wildtype cells not lysogenic for the phage, to use for the lawns.
4. Incubators at 34°C and 40°C.
5. Melted 'top agar' (0.7 % agar medium) at ~48°C.
6. Normal agar plates at room temperature.

Recombination procedure:

1. Mix:  0.3 ml cells with about 10^9 phage of each type, both phage together and each separately.
2. Incubate for 10' at 34°C.  This gives the phage time to attach to the cells and inject their DNAs.
3. Pellet the cells, resuspend them in medium, and pellet them again.  This washes away all the phage that didn't infect the cells.
4. Resuspend the cells, diluting them 1/300 in culture medium.  
5. Set aside some of this culture (room temperature) to assay for 'infectious centres'.
6. Shake this culture for 90' at 34°C.  This time allows the phage to complete one cycle of infection.  The infected cells will burst, releasing the progeny phage.
7. Add  a few drops of chloroform to the culture to kill the remaining cells, and centrifuge the culture to remove dead cells and debris.  Transfer the supernatant ('lysate') to a fresh tube.

Assaying the results:

1. Put about 0.1 ml of the wildtype culture (about10^8 cfu) into each of a series of numbered glass culture tubes, ideally at 30-34°C.
2. Dilute the phage lysates or the set-aside culture in culture medium.
3. Add 0.1 ml diluted or full-strength lysate to each culture tube.
4. Incubate 15' at 34°C.  This allows phage to attach to cells and inject their DNA.
5. Add 5 ml top agar (2.5 ml?) and pour onto the appropriate numbered plate, rocking to quickly spread the top agar before it sets.
6. Incubate the plate at 34°C or 40°C overnight.
7. Count plaques.  
8. For the lysates, the recombination frequency is the titer of plaque-forming units at 40°C divided by the titer at 34°C.  For the set-aside culture this ratio gives the proportion of infected cells that produced recombinant page.

To get the true recombination frequency requires titering the lysates, but in the old experiment I'm looking at (#125) the frequencies of infectious centres that contained recombinants were reliable indicators of the recombination frequencies in the lysates.  For log phase cells, 2 x 10^-6 of the phage in the lysate were recombinants and 5 x 10^-4 of the infectious centres contained recombinants; for competent cells the numbers were1.9 x 10^-3 and 1.7 x 10^-2 respectively.  So maybe I can just plate the infectious centres.  I'll try both the first time and see if the correlation is reproducible.

One concern with plating the infectious centres is that recombination may occur in the wildtype cells in the lawns.  The opportunity is there because every mixed-infection cell will release a mixture of phages that may multiply infect neighbouring cells.  However these cells aren't competent so phage recombination is probably not a concern.  If the background is high I could use rec- cells for the lawns.

Clean boring results

OK, I've done the third of the experiments I planned here, and the results cleanly show that nothing interesting is going on (at least nothing interesting that warrants investigation).

I wanted to know if the peculiarities I had long-ago noticed in DNA of competent cells were reproducible.  So yesterday I grew some wildtype cells in rich medium.  Some of them I collected during exponential growth ('log phase', cell density about 2 x 10^9 cells/ml), some when the culture was approaching its final density ('stationary phase', about 10^10 cells/ml), and some I transferred to the competence-inducing starvation medium while they were in log phase.  I prepared chromosomal DNA from all three treatments, and then incubated it either in the standard DNA buffer TE (10 mM Tris pH 8, 1 mM EDTA) or in the mung bean nuclease buffer that had previously given anomalous results for competent-cell DNA.  DNA in the mung bean nuclease buffer sat at room temperature for about an hour, with and without being heated to 65 °C for 10 minutes.  Then I ran all the DNAs in a gel to check their condition.

You can see that there's no significant differences between the effects of the treatments on the different DNAs.  The competent cell DNA is in slightly shorter fragments (the biggest marker band is 29 kb), but the difference between it and the other DNAs isn't changed by the MBN buffer.  Heating the DNAs in the buffer causes the usual streaking of the bands (caused by having a lot of high-molecular-weight DNA running at the same position) to be a bit blurry, but again that applies equally to all three DNAs.

So I can put this old result out of my mind, and get to work on my planned competence and phage recombination assays.

At Northern Voice

More people than I expected, more diverse, and much more enthusiastic than the scientific meetings I usually go to.

Ancient mutants

While searching the -80 °C freezer for a missing chemical I discovered a box of H. influenzae competence mutants from 1970.  Well, I didn't freeze them in 1970, but they were originally isolated in 1970 (Castor, Postel and Goodgal, 1970 Nature 227: 515-517).  The paper gives specific information about only a few of the mutants they isolated, but the strain names go up to com-110 and a later paper refers to 70 independent isolates with abnormally low transformation frequencies.

Unfortunately, none of the strains I found (com-14, -15, -22, -23, -34, -37, -45, -47, -51 and -89) were mentioned in the 1970 paper.  If this had been a new paper, the data for all the mutants wold have been in a supplementary (online-only) table), but not 40 years ago.  So I tracked down later papers from the same group, hoping to find more information about the mutants.  I did find follow-up papers, but not much about the particular mutants I have.  One mutant (com-47) was included in a set whose DNA uptake and recombination were investigated in more detail; it takes up some DNA but not as much as wildtype.  None of these mutants were included in a group whose sensitivity to DNA damage was studied.

One of the mutants, com-51, did get a paper all to itself (Concino and Goodgal 1982  J. Bacteriol. 152:441-450).  The paper reports that the mutant cells produced normal or near-normal amounts of membrane-associated DNA-binding material when competence was induced, but this material did not remain on the cell surface.  Instead it was released into the culture medium as membrane vesicles.  The data doesn't look particularly compelling - for example, the culture medium from these cells is reported to bind H. influenzae DNA (721 cpm of 3H-DNA) but not E. coli DNA (0 cpm), but 721 cpm is only 50% above the H. influenzae DNA background (1431 cpm).  But the mutant might be useful for our work on uptake proteins and uptake specificity, even though we don't know anything about the responsible mutation (or mutations - the cells were heavily mutagenized).

In a 1981 paper the authors also characterized this mutant's phenotype and examined the cell-surface proteins it produced when competent.  Its DNA uptake was 3% of wildtype, and transformation was undetectable (<5x10^7).  The gel  analysis of iodinated surface proteins doesn't show any significant differences between wildtype and com-51.

My experiments: might I have a plan?

Classes have been over for a month and I have yet to do an experiment!  For shame.  But after going over everyone else's projects I think I have a clear idea of what I should be doing.

1. Measure starvation-induced competence for each of the competence-gene knockouts:  This will be replicating measurements done by an undergraduate over the past 6 months.  I'll just do each strain once, provided my results agree with hers.  I'll also freeze some of the competent cells.

2.  Assay phage recombination in the competent and non-competent mutant cells:  Old experiments using temperature-sensitive mutants of the H. influenzae temperate phage HP1 showed that recombination between the ts loci is more frequent in competent cells and completely dependent on the host RecA pathway (undetectable in a rec1 mutant).  Phage recombination is much more efficient in competent cells than in log-phase cells; this is true both when competence is induced by starvation of wildtype cells (in MIV medium) and when it is induced by the presence of the sxy1 hypercompetence mutation (in rich medium). 

But phage recombination is unexpectedly blocked by a rec2 mutation.  (The baroque history of rec2 is described in this post.)  The rec2 mutant also does not have the peculiar DNA aberrations described in competent cells (more below about these).  So I'm wondering if phage recombination can give us a transformation-independent window into DNA metabolism in competent cells.  Hence my plan to test all the mutants.

The recombination assays are simple in principle: just infect cells with a mixture of two ts phages (ts1 and ts3), each unable to form plaques at 40 °C.  The infections are done at the permissive temperature (34 °C), but the resulting lysates are titered at both 34 °C and 40 °C.  The ratio of plaque-forming units (pfu) gives the recombination frequency.  But in practice they're fussy.  I need to have incubators at both temperatures, which will take some arranging as we only have one incubator at present, set at 37 C.  I also need to fuss with getting the temperature control just right, as H. influenzae is pretty picky about this, and to make lysates of the mutant phages that have sufficiently high titers that I can do mixed infections (need more phage than cells).  To make these lysates I need to grow up the lysogens carrying the wildtype and mutant phages, and so I first need to find out whether they survived the big freezer meltdown of 2005.  I may also need to buy fresh mitomycin C to induce the phage - our stock has been stored in the freezer but it's more than 20 years old.

While I'm surveying competent wildtype and mutant cells I'm going to revisit an unsolved old problem - the unusual structural features of DNA in competent cells.  This was first reported by Leclecrc and Setlow in 1975, based on studies using denaturing sucrose gradients which suggested that the chromosomal DNA of competent cells had single-stranded regions, such that when denatured the average fragment length is about 200 kb (if I've correctly converted 5x10^7 Daltons to kb).  David McCarthy later used electron microscopy to examine competent cell DNA; he found single-strand gaps and 'tails' in DNA from competent cells.  The gaps were not seen in a rec2 mutant, but the tails were seen in both rec1 and rec2 mutants.  As a post-doc I tried to investigate this, using high molecular weight DNA purified from log-phase and competent wildtype cells.  I incubated the DNAs with Klenow and 32P nucleotides to tag any gaps - this labelled the DNAs of competent cells and log-phase cells identically.  DNA from stationary-phase cells was labelled less, presumably because of the absence of replication forks.  I also tried digesting the DNAs with nuclease S1, which preferentially cuts single-stranded DNA, but I had very odd results, as the competent-cell DNA migrated very strangely after incubation with the special buffer used for S1 nuclease (NaOAc ph 4.5 10 mM Zinc, 1.5 M NaCl).  It's this strangeness that I now want to revisit, so I'll just make DNA from competent and log-phase cells the usual way, incubate it with this and other buffers, and run it in gels with and without restriction digestion. 

The Research Associate's experiments, part 2

The second big component of the Research Associate's recent work is on regulation of (and existence of) competence in E. coli.  (The rest of her work is described in the previous post.)  We've shown that E. coli has homologs of all but one of the genes known to be needed for competence in H. influenzae, and these genes are induced when the competence-specific regulator Sxy is artificially induced.  BUT, we haven't been able to detect transformation, and we don't know of any conditions that naturally induce Sxy.  Because Sxy in E. coli appears to work very similarly to Sxy in H. influenzae, we're also hoping that some questions will be more easily answered in E. coli, which is a more tractable system.

Questions:  I.  About the regulation of Sxy expression in E. coli

Q. 1:  How is transcription of the E. coli sxy gene induced? 

We don't know.  Nobody knows.  See previous posts.

Q. 2:  Is the E. coli sxy gene post-transcriptionally regulated?

First, we needed to find the 5' end of the sxy transcript?  The RA has now mapped this (after some strenuous battling with experimental artefacts).  It's well upstream of the start codon (~100 nt?), as is the case in the Pasteurellaceae and in Vibrio cholerae.  So there's lots of potential for post-transcriptional regulation, as has been shown in H. influenzae and V. cholerae.

Prediction of secondary structure of the mRNA sequence using the program mfold shows that it can fold into complex secondary structure, but we'd need experimental evidence to show that this structure is biologically significant (mfold will fold just about anything).

Questions:  II.  About what E. coli Sxy protein does for E. coli

The results of the experiments described below are quite consistently negative, so the RA's strategy is to cover all the possibilities so we can at least write a solid negative-result paper.

Q. 3:  How does Sxy stimulate transcription of genes with CRP-S promoters?

CRP-S sites are variant CRP sites where transcritional activation requires both CRP and Sxy.  We have published genetic evidence that stimulation of transcription at CRP-S sites depends on direct interaction between the CRP and Sxy proteins - assays using cross-complementation between H. influenzae and E. coli induce transcription much more strongly if the CRP and Sxy proteins both come from the same species.  We also have unpublished evidence.  In vitro, far-Western blots show that CRP and Sxy physically interact, and pull-down experiments show that pulling down Sxy brings down CRP.

But Sxy doesn't bind to CRP-S sites in bandshift experiments (in vitro) whether or not CRP is present, and adding Sxy doesn't improve CRP's poor ability to bind to them.

A plan?  Construct a fusion of the candidate regulatory parts of the sxy gene (= promoter, 5' untranslated region and 5' part of the coding sequence) to a reporter gene.  Then mutagenize the sxy part and screen for changes in expression.  The mutagenesis could be done randomly with degenerate PCR oligos (???) or be site-directed.  Changes in expression would give clues about regulation, and any high-expression mutations could be tested for induction of transformability (see below).

Here's another idea.  How about we put the E. coli sxy gene, with all its candidate regulatory sequences, into a H. influenzae sxy knockout, mutagenize the regulatory region by transformation with a degenerate sxy PCR product of some sort, and then select for hypercompetence mutants as we did to get the original H. influenzae sxy mutants?  Then we can sequence the sxy genes to find mutations that increase expression (or activity).  I suppose the E. coli genes could be on a plasmid (or plasmids) rather than in the chromosome.  I can't remember whether we've shown that E. coli sxy complements a H. influenzae sxy knockout - it should, based on the E.coli experiments.

We should also just first do a time course etc. to see how replacing the Sxy gene changes induction.  For the time course we'd probably want to put the E. coli CRP gene in too, so we'd get higher induction of the CRP-S genes and thus more sensitive transformation assays.

Questions:  II.  About what the E. coli CRP-S regulon does

Q. 4.  Will expression of E. coli Sxy ever induce transformation in strain K-12?

The RA has developed an assay for chromosomal transformation in E. coli, using chromosomal DNA of a strain carrying a KanR insertion in the crp gene, or a TetR insertion in the purE gene.  Sxy is artificially induced, from either a high-copy plasmid or a low-copy plasmid.  BUT, the big problem is that we have no positive control - we don't have any conditions or genotypes where giving cells this DNA does produce transformants.  Transformation requires both that the cells take up DNA and that the DNA recombines into the chromosome.  In H. influenzae transformation is a very sensitive assay for DNA uptake because the recombination is quite efficient.  But in E. coli we have no idea whether transformation would be a usual outcome of DNA uptake.

One solution is to artificially enhance the efficiency of recombination by turning on the phage-derived recombineering genes she's been using to create mutations.  In principle this means we only need to assay for uptake.  So she's done this, inducing the recombineering genes by heat-shock (they're in the chromosome under the lambda CI857 ts promoter).  The target for recombination is the H. influenzae comM gene on a plasmid, and the recombining DNA is a PCR product (i.e. dsDNA) of a comM::SpcR fragment.  When the SpcR fragment is introduced into the cells by electroporation, she gets thousands of transformants.  The cells also contain an IPTG-inducible sxy gene, and when this is induced along with the recombineering genes, she gets a few SpcR colonies without electroporation.

Are these natural transformants?  She wants to rule out the possibility that the temperature shock used to induce the recombineering genes somehow allows some SpcR DNA to get into the cell.  She's going to do this by using a different recombineering strain, one where the phage genes are on a plasmid and induced by adding the sugar arabinose rather than by heat shock.  Another advantage of using this strain is that, if she gets what appear to be transformants, she will be able to test the effect of knocked-out competence genes by simply moving the recombineering plasmid to one of our Keio strains carrying chromosomal competence-gene knockouts.

However we still need to worry about the difference between single-stranded and double-stranded DNA coming into the cell - I think the recombineering proteins handle these very differently.  One control would be to denature the PCR product by heating it before giving it to the cells.

She's also tried inducing sxy in the  K-12 strain that Steve Finkel used to show that (1) E. coli cells can take up DNA and use it as a nutrient, and (2) this uptake needs homologs of H. influenzae competence genes.  In principle we know that this strain can take up DNA, but our visiting student last year was unable to replicate this result.  In an case, this strain did not transform with her marked chromosomal DNA.

Q. 5.  Does expressing Sxy promote recombination?

She also tested transformation by electroporation without inducing the recombineering proteins.  Whether or not Sxy was induced, she saw no transformants.  This tells us that Sxy does not activate recombination pathways.


Q. 6.  Does providing the H. influenzae pilF2 gene enable E. coli K-12 to transform when Sxy is induced?

The only H. influenzae gene needed for competence that's not in E. coli (K-12 and other sequenced strains) is pilF2.  It's in all competent Pasteurellaceae and in Vibrio cholerae.  (I'm sure I already wrote this somewhere but I can't locate it now.)  She's provided it on the sxy expression plasmid, both under its own promoter and under the IPTG-inducible promoter, but these cells didn't transform either.

Q. 7.  Will expression of E. coli Sxy ever induce transformation in non-K-12 strains?

She's tested many strains of the ECOR collection (a reference set of diverse E. coli strains isolated from many different locales and hosts) for transformation during growth and stationary phase in the rich medium LB, using her chromosomal DNA (probably crp::KanR).  No transformants were seen.  She also tested the cultures for expression of the Sxy-induced pilin protein; none was produced.  With the help of a summer volunteer undergrad she's now going to put an inducible sxy plasmid in these strains and retest them.

Q. 7.  Does expression of E. coli sxy and the CRP-S regulon provide E. coli with benefits other than competence?

The RA hasn't been working on this specifically, but we need to think about it if her results continue to be negative.  If it's true that E. coli cannot take up DNA by the natural competence mechanism, why does it have intact versions of all the necessary genes except pilF2, under a Sxy-controlled CRP-S regulon?  If these genes were just leftovers from a competent ancestor, we would expect to see some loss-of-function mutations in them, if not in K-12 then in some of the other sequenced strains.  (Has anyone checked the alleles in the other sequenced strains?)

How carefully have we checked the phenotype of the E. coli sxy knockout?  Might it be defective at anything?  In the RA's E. coli sxy paper (2009) we compared long-term survival of wildtype and sxy-knockout cells in LB.  The mutant reached the same initial cell density as the wildtype, and it survived long-term culture just as well.  But it did not compete equally with wildtype when the two strains were cultured together, a phenotype that Steve Finkel's work suggested was due to inability to sue DNA as a nutrient.

The Research Associate's experiments, part I

While I've been paying attention to other things (teaching, writing, proposing), the Research Associate has been doing a lot of work on the projects we're funded to do.  Below I'll highlight in purple the experiments that I might take on.

Recombineering:  The goal was/is to create marked (selectable for antibiotic resistance cassette) and unmarked deletions of all the H. influenzae competence genes.  This has required an enormous amount of work, much more than was originally expected.  The last step, converting the marked mutants to unmarked, turned out to be particularly troublesome because the counter-selection doesn't work in the standard lab strain.

But I think we now have marked knockouts of every gene in the competence regulon, but unmarked mutants for only some.  These are on the back burner for now, though she's still creating knockouts of comI and comJ (implicated in competence though not regulated by it) and mutS (for study of recombination).  She also knocked out the sxy gene of a related species, Actinobacillus suis, for a collaborator.  One project for me is to follow up on the characterization of these competence mutants (begun by an undergrad), rechecking their starvation-induced transformation frequencies.

Competence differences in H. influenzae strain 86-028NP ('NP'):  This is the low-competence strain the postdoc is using for his sequencing of recombination tracts and the planned mapping of genes responsible for competence differences.  The RA noticed that, although this strain has homologs of all the genes known to be needed by H. influenzae strain Rd for transformation, it lacks several competence-induced genes with unknown functions.  So she's putting the Rd genes into the NP chromosome to see if this changes their competence.  This should be easy as she already has the Rd genes cloned in the recombineering vector, and the counter-selection that fails in Rd works fine in NP.


Regulation of competence by purines and purine nucleotides:

The big project that's most important is understanding how purines affect competence in H. influenzae.  The new work on this project has two fronts, repression of CRP-S genes by PurR and post-transcriptional control of Sxy expression by purine nucleotides.

Front 1, regulation by PurR:  The lesser front is finding out whether the purine repressor PurR affects transcription of any competence genes.  When one of the purines guanine and hypoxanthine is available, they bind to PurR and enable it to bind its recognition sequence.  This sequence is present in the promoters of most genes involved in de novo synthesis of purines.  I initially thought it was also present in the promoters of several CRP-S genes but the RA and others have analyzed this more rigorously and find that the only strong candidate is in the rec2 promoter.

Our previous work on the role of PurR in competence has been compromised by problems with what we thought was a good PurR knockout strain.  First we found that strains had been mixed up, and ten that the knockout didn't remove the part of the gene that codes for the DNA-binding domain of PurR.  Now the RA has made a clean mutation that removes the whole gene.  She's also knocked out the purH gene; this gene codes for the last step in purine synthesis, and the knockout allows us to disassociate competence effects due to PurR regulation from effects due to synthesis of purines.  She's put the two knockouts together and also combined them with some sxy-hypercompetence mutations (see below).

One simple way to test for PurR regulation of rec2 is using some fusions to the E. coli lacZ gene, made years ago by Michele Gwinn.  We have her fusions to two CRP-S genes, comA and rec2 - comA makes a good control as it doesn't have a candidate PurR site.  The RA has made the purR- derivatives of these fusion strains and tested them in rich medium, using cells in log phase, at the onset of slowed growth, and after overnight culture.  None of the conditions showed much difference in expression of the fusions with or without PurR.

...pause while I diagram what we should expect...  First, we expect PurR to be active (repressing) throughout growth in sBHI, because our microarrays showed no induction of PurR-repressed purine genes.   We also expect little or no expression of comA, rec2, and the other competence genes (CRP-S genes) in log phase, because sxy is not transcribed much or translated efficiently.  When growth slows we expect low-level expression of the CRP-S genes.  If PurR represses rec2, we expect to see higher beta-galactosidase expression in the purR- rec2 fusion strain than in its purR+ control.  But she didn't see that. 

This might mean that PurR doesn't regulate transcription of rec2.  But the expression levels of the fusions were very low (mostly less than 40 Miller units, whereas starvation-induced cells produce several thousand units).  It would be good to repeat these experiments after adding cAMP to all the cultures to give higher expression of the CRP-S genes; if we don't see any effect of PurR, probably there isn't much effect.  She's now also done careful measurements of the baseline expression of these fusions, data we need to interpret the results of whatever manipulations we now do.  I don't know if we've ever monitored the effects of cAMP on expression of these fusions in rich medium - it might be easier to just do it now than to find out whether we've already done it...

The presence of a functional purine-biosynthesis pathway in these cells shouldn't have mattered, but the purR- cells did differ from the controls in this, so it would be good to repeat the experiments with the purH knockout added to all strains. 

Another way to test for PurR repression of rec2 would be to put the H. influenzae lacZ fusions into E. coli, where it will be easier to test the effect of PurR and purines (because we can grow cells with and without various purines.  Unfortunately we don't have plasmid clones of the fusions, just  H. influenzae chromosomal fusions.  The RA thinks it might be easiest to just remake the E. coli fusions rather than cloning them from the H. influenzae chromosome, but I think that at least one of the fusions is a simple integration of an E. coli plasmid.  These cells should contain a low frequency of excised plasmid - if so, simple transformation of E. coli with a cell lysate might give the desired plasmid clone.

Another test would be direct assay of bandshifting.  The RA wondered if we might be able to get purified PurR protein (E. coli) from someone.  But I just looked at the old E. coli PurR paper (1988); they did bandshift assays using crude cell extracts, so maybe we could do that too. 

We also want to know how widespread competence regulation by purines is in other Pasteurellaceae.  The RA has found that the putative PurR binding site is also present in the rec2 promoters of other Pasteurellaceae, and E. coli.

Front 2:  Regulation of sxy expression: 

The RA has confirmed and extended our previous work showing that purine nucleotides (AMP and GMP) prevent competence development in starvation medium.  Most of that work used quite high nucleotide concentrations (5 mM), and some of our experiments found that these were high enough to inhibit cell growth.  So she's meticulously repeated these using concentrations of 1.0 and 0.1 mM AMP (3 replicates).  1.0 mM was enough to reduce transformation by 500-fold, and 0.1 mM by 40-fold.  But the 1.0 mM AMP also inhibited cell growth - cells usually double once after transfer to the starvation medium, but their numbers didn't significantly increase in 1.0 mM AMP.  Cells transferred to starvation medium with 0.1 mM AMP doubled normally.  This is excellent, as it gives effects on competence at concentrations that are unlikely to cause other problems.  But I'd still like to have some better controls, to confirm that the competence effects we see are really directly due to specific effects on competence genes, not to more widespread effects.  One possibility is to use a CRP-N-regulated gene (not responsive to Sxy) as a control.

She's done similar experiments in two other competent Pasteurellaceae, Actinobacilus pleuropneumoniae and A. suis.  Our collaborators have found strains of these species that transform at sufficiently high frequencies that the effects of added purines could be tested, and the RA has shown that AMP reduces their competence in the same way as in H. influenzae.

She also tested the new purR knockout (in H. influenzae).  Its transformation frequency in starvation medium is down 5-fold.  This may be because the cells are constitutively synthesizing their own purines and so are less 'shocked' by the sudden absence of purines from their surroundings.  They were also less sensitive to addition of AMP;1.0 mM AMP reduced transformation only 10-fold, and 0.1 mM had no effect.  This reinforces the hypothesis that sudden purine depletion contributes to competence induction, and that enrichment of the starvation medium with AMP decreases competence directly and not by some general perturbation of metabolism or gene expression.

These effects were reduced when the cells carried sxy-hypercompetence mutations that increase the efficiency of translation of sxy mRNA.  1.0 mM AMP reduced transformation of a sxy1 mutant only 20-fold, and 0.1 mM no more than 2-fold.  She's done 3 replicates so this is a solid result.  She also tested a couple of our other hypercompetence mutations; in both of these she only tried 0.1 mM, and saw no effect on transformation.  This is consistent with our hypothesis that AMP acts by preventing translation of sxy mRNA.  She has saved cell pellets of all the competent-cell preps she used, so these can be assayed for expression of Sxy.  An excellent control would be to assay the pellets for presence of some other protein that's induced by the starvation regime but not regulated by Sxy.  Again, one of the cAMP-induced CRP-N-regulated proteins would be good, but we'd have to make our own antibody first (either purifying the protein or specifying a synthetic peptide).

She's also modified our antibody-based assay (Western blot) for Sxy.  The grad student who developed it used a detection method that was very sensitive, but his blots had very high background.  She's found that, with a less-sensitive assay, the Sxy bands are still very clear but the background is greatly reduced.  It's not entirely eliminated, which is a good thing because the few background bands serve as excellent controls for normalizing the band intensity (provided, of course, that their proteins aren't altered by the starvation regime).


E. coli competence:

This is the second big research problem the RA has been working on.  I'll leave this for a later post.