OK, plasmid transformation does work in H. influenzae...

At least it worked for me, for one of the DNAs I tested.  But the results weren't very clean or very well controlled so I need to do the experiment again.

This time I'll use two different preps of the same shuttle vector pSU20 - one prep of plasmid grown in E. coli and one of plasmid grown in H. influenzae.  (I would have done this the first time but couldn't find a H. influenzae-grown prep.  Today I streaked out the right cells from our freezer stocks, and tomorrow I'll make a plasmid prep for this experiment.)

I expect the E. coli-grown plasmid to transform quite poorly, because the DNA will lack methylation at the HindII and HincII restriction sites.  In my first experiment the difference was dramatic: I got 10,000 transformants into E. coli but none into H. influenzae.  The Rd strain of H. influenzae carries both of these restriction systems (Ham Smith got a Nobel Prize for discovery of these), and its cytoplasm is chock full of the HindIII and HincII restriction enzymes.  Although its own DNA is appropriately methylated and thus immune to cleavage, incoming DNA from other species is cut.  The restriction enzymes only cut double-stranded DNA so they don't affect chromosomal transformation (watching the DNA uptake movie might help this make sense), but plasmids introduced by electroporation or plasmid transformation remain double-stranded, so they're vulnerable.

I'll also use E. coli-grown and H. influenzae-grown preps of the noviobiocin-resistance plasmid pRRnov1.  In my quick-and-dirty experiment I used a very old tube of this plasmid, grown in H. influenzae.  This gave about 100 transformants into H. influenzae but none into E. coli.

Thinking about the impact of endogenous restriction enzymes prompted the postdoc to wonder if this might be a limiting factor in the RAs' recombineering work - it might help explain why her attempts to make 'unmarked' deletion mutants sometimes succeeds and sometimes fails.

First, my understanding of the process she uses:

She starts with mutant cells she's created - in these cells a specific competence gene has been deleted and replaced with a cassette giving resistance to spectinomycin.  Because this cassette can disrupt expression of downstream genes she wants to excise it from the chromosome, leaving an 'unmarked' mutation.

To excise the SpcR insert, she first electroporates a plasmid with the flp recombinase (pRSM2947?) into the H. influenzae cells carrying the SpcR-marked mutation.  The SpcR cassette is flanked by DNA sequences that that are cut and rejoined by the Flp enzyme, excising the cassette.  The plasmid is also temperature-sensitive (Ts) so cells must be plated at 30°C.  If this electroporation works (sometimes it doesn't, perhaps due to restriction)) she gets H. influenzae cells that carry the excision plasmid.  

She then induces the excision genes (by adding tetracycline), plates the cells, and screens for colonies that are now SpcS.  Plating at 37°C ensures that the cells also lose the Ts plasmid.  Sometimes the induction works well (more than 1% of the colonies are SpcS) and sometimes it doesn't work at all.

So the other day the postdoc pointed out that restriction and subsequent repair of an E. coli-grown plasmid transformed into H. influenzae might sometimes produce defective versions of the plasmid, versions that are able to replicate and that confer the expected antibiotic resistance but that have defects in other plasmid-borne functions.  

When the RA electroporates pRSM2947 into the marked mutants, I think she uses a plasmid stock that was grown in E. coli.  Cleavage of this plasmid by the endogenous restriction enzymes might sometimes give plasmids with defects in the flp recombinase gene.  These cells would then fail to produce any unmarked derivatives on induction with tetracycline.  Even if she routinely checks the transformants for presence of the pRSM2947 plasmid, she might not detect that the plasmid now has a defect.  So maybe one way to improve the efficiency of the excision process is to start with a stock of pRSM2947 that has been grown in H. influenzae. 

How is this work going to be useful for our upcoming grant proposal, you might ask?  I'm asking myself that too.  More on this later.

Update:  The RA tells me that she switched to using H. influenzae-grown plasmid a while back, but that this didn't solve the excision problems.

Does plasmid transformation work in H. influenzae?

The word around the lab is that the standard technique for transforming H. influenzae cells with plasmid DNA hasn't worked for anyone in years, so I'm testing it myself.  It always worked OK for me, but I haven't done it in a long time.  The technique is simple: cells are made naturally competent in the usual way (starvation in MIV medium) and incubated with plasmid DNA.  The plasmid DNA is efficiently taken up into the periplasm, but it can't get across the inner membrane because that translocation needs a DNA end and the plasmid is circular,  The cells are then given an osmotic shock (30% glycerol for 10 minutes), which somehow drives the plasmid into the cytoplasm.

Why do this now?  Lord knows I have lots of other stuff to deal with, but plasmid transformation is potentially something we'd want to include in our upcoming CIHR grant proposal, preferably with some preliminary data.  The only major concern raised by the reviewers of our previous submission was that we didn't propose to evaluate the effects of point mutation changes in competence genes, just of deletions of the whole genes.  The RA has developed a very nice way to make point mutations in genes cloned in E. coli, but we don't have an efficient way to transfer them into the H. influenzae chromosome.  Well, we can transfer them into the chromosome by transforming competent H. influenzae cells with the mutated DNA, but this is only efficient if the DNA fragment is quite long (see this post), and finding the desired transformants requires laborious screening because there's no associated selectable marker.  We're in the process of making a suitably long fragment of an interesting mutation she's generated, and I hope to be able to test this in the next week or two.

But the post-doc pointed out that we should also consider ways of testing point-mutation changes borne on plasmids, because these can easily be selected for.  The strategy would be to test cells containing the mutant plasmid and a deletion that removes the chromosomal copy of the gene.  One complication is that the plasmid-borne competence gene must have a promoter to drive its expression - ideally this will be its own competence-regulated CRP-S promoter.  I'll have to check whether the short cloned fragment containing the RA's interesting mutation includes its promoter - if not, the longer versions will.

In most cases we'd be working with a gene that is essential for natural competence, so there are two ways to construct these strains.  The first is to start with the strain carrying the chromosomal deletion and introduce the plasmid by electroporation.  The RA has found that electroporation sometimes works very well and sometimes doesn't work at all - I don't know if she's ruled out the effects of the restriction enzymes in the H. influenzae cytoplasm, which are expected to cut up DNAs containing unmodified HindIII and HincII sites.  The second way is to start with competent wildtype cells, introduce the plasmid by plasmid transformation with selection for the plasmid vector's antibiotic resistance, and then introduce the deletion by normal chromosomal transformation with selection for the inserted spectinomycin-resistance cassette.

I think this work needs a lot more thought, and soon, because the grant proposal deadline is Sept. 15.  But last night I did a test of the basic plasmid-transformation method, using several DNA preps of plasmids based on the chloramphenicol-resistant shuttle vector pSU20 (two very old, and one new but of plasmid grown in E. coli).  I transformed them into both competent H. influenzae and competent E. coli (as a control).  I'll get the E. coli results today, but will have to wait till tomorrow for the H. influenzae results because the colonies grow very slowly on chloramphenicol plates.

We now resume our #arseniclife blogging...

When we paused last week, I had just noted the unexpected result that, in two of three tests (#1184 and #1189), GFAJ-1 cells in 3 µM PO4 + 40 mM AsO4 grew to a higher density  than the cells in 3 µM PO4 (no AsO4), but the cells with more and with less phosphate didn't grow much at all.  In the other test (#1188) the cells didn't grow at all in the arsenic cultures; I won't say anything more about these cultures unless I get more results like this.  All cultures without arsenic grew as they had in previous experiments.

I left the #1189 arsenic cultures in the incubator while I was away, and over this ~225 hr incubation the 1.5 mM-phosphate' and no-added-phosphate cultures grew to densities close to those of their no-arsenate controls.  I don't know why they grew so much slower than the 3 µM phosphate+arsenate culture.

I'm going to repeat these cultures once more.  If I see the same results (fast high growth of cells in 3 µM phosphate + arsenate), I'll dilute the 3 µM phosphate cultures into 400 ml of the same medium ± arsenate, to get lots of cells for my first arsenate-grown DNA prep.

SciFoo!

What's SciFoo?  Science Foo Camp, of course!  (Here are links to Wikipedia and Twitter.)  You've probably never heard of this 'unconference' - it's small, you need an invitation, and nobody talks about their data.

It happens at the Googleplex (Google's headquarters in Mountain View California.  About 200 people, mostly scientists but also journalists, artists and teachers, gathered for two days of high-quality conversations.  Some of the conversations happen in specific blocks of time, and the rest over meals and drinks and demos and just hanging around.  Much more like a series of wonderful dinner parties than like a typical scientific meeting.

The bike is part of Google's fleet (photo from aemkei's Flickr photostream).  I was going to take one for a spin, but they're 'fixies' (fixed-wheel, no brakes) and I didn't think my cycling skills were flexible enough to save me from crashing when I wanted to stop.

Polishing my SciFoo talk - last slide

My 5-minute 'Ignite' talk at SciFoo is tonight, and I still need to work out the point I'll make with my last slide.  (It's too late change the slide - our Powerpoint files had to be submitted two days ago.)

I'll have just said that big mistakes were made by everyone involved (authors, reviewers, editors, publicists, journalists).  Then I want to say something about how scientists in particular need to be able to admit their errors - we're working not only at the frontiers of knowledge but at the frontiers of our abilities.  Failure to admit we've been wrong is a betrayal of the scientific process.

Can I say that in 15 seconds, without rushing my words?  Maybe, but it would be better to cut a few words, or at least a few syllables.

How about this?

Previous slide:  Everyone involved made big mistakes (authors, reviewers, editors, publicists, journalists).  But the big betrayal wasn't the errors but the failure to admit them.

Last slide:  Scientists work not only at the frontiers of knowledge but at the frontiers of our abilities, and learning to be wrong should be part of our training.

A good paper, but is it 'astrobiology'?

A while back I asked for examples of good astrobiology papers.  After a bit of back-and-forth with some commenters, I clarified my search:  I was looking for papers that reported competent experimental research and self-identify as 'astrobiology'.  And I was looking for personal recommendations to papers that had been read by the person recommending them, not just pointers to journals or reports where I could read astrobiology papers and decide for myself whether they were any good.

The results were disappointing.  The problem wasn't that the commenters recommended papers that turned out to be lousy, but that they didn't recommended any recent papers at all, except for a reanalysis of Miller's original spark-discharge material from his 1953 experiment.  The problem wasn't that the commenters were ignorant of the field - one was the Director of the NASA Astrobiology Institute, who directed me to a recent report on the Institute's success but didn't give personal recommendations for any of the publications it lists.

I'm thinking about this issue now because of a paper that just appeared in PNAS, titled Carbonaceous meteorites contain a wide range of extraterrestrial nucleobases (authors Callahan et al.).  CNN's Lightyears blog headlines this as DNA discovered in meteorites, but most reports were more sensible.  (The image below is from the Lightyears blog.)

To my non-expert eye this looks like good science.  The results are not really surprising (purines have been found in meteorites before), but they're very solid.  What makes this work important is that the authors surveyed a wide range of meteorites, carefully eliminated sources of external contamination with terrestrial purines, and showed that the distribution of purines found in the meteorites matched that produced by laboratory reactions simulating space chemistry but not that of terrestrial contaminants (e.g. they found not only the common terrestrial contaminant adenine but also 2,6-diaminopurine).

So is this good paper a good astrobiology paper?  I don't think it qualifies.  Although most of the authors are supported by NASA, they nowhere mention astrobiology or consider whether their work has implications for the origins of life anywhere but on Earth.  

(I'm officially a zoologist, so now I'm off to the San Francisco Zoo, planning to be back in time for the SciFoo meet and greet this afternoon.)

Preparing my Ignite talk for Science Foo Camp

I'm allowed 5 minutes and 20 slides (15 seconds each) to tell the #arseniclife story to about 250 scientists at Science Foo Camp on Saturday.

I'm hand-drawing the slides, so as to have simple appealing illustrations rather than dense data.  This is taking ages as I lack both the artistic skills and the technical skills to do it efficiently, but I think it will be worth the effort.  Fitting everything smoothly into 5 minutes also takes a lot of practicing - luckily each practice takes only 5 minutes.

Control DNA preps for my mass-spec colleagues to test

I've got lots of GFAJ-1 cells in the fridge, so I think I'll make some DNA preps from them to send to my colleagues at Princeton for the initial mass-spec measurement of baseline levels of arsenic.  They've done the initial controls, determining that their setup's detection limit is about 1-^-7 - 10^-8 M arsenate, equivalent to replacement of about 0.01% of the phosphates in the DNA backbone with arsenate.  This is about 300-fold lower than the 4% replacement claimed by Wolfe-Simon et al.

The cells were grown in AML60 medium with either limiting or ample phosphate - I don't think it matters which.  I'll do one DNA prep with the limiting-phosphate cells.  As a control for carry-over arsenate contamination, I'll add sodium arsenate to the other culture (40 mM) and let them steep in it for a little while, then wash away the arsenate and do another DNA prep.  I'll also take some purified DNA, soak it in 40 mM arsenate for a little while, and then repurify it.  If my DNA purification methods are good, none of the DNAs should have detectable arsenic.

Growth of GFAJ-1 in 40 mM arsenate (not)

My initial attempts to grow GFAJ-1 in media containing 40 mM sodium arsenate have given unexpected results.  The first time I thought it might be a screw-up on my part, but the second time suggests a problem with the cells.

The experimental design is simple.  I set up the six flasks shown below, and inoculated each with about 2 x 10^4 GFAJ-1 cells/ml.  If we ignore the presence of glutamate in the medium, flask 1 corresponds to the +P/-As condition of Wolfe-Simon et al.'s Fig. 1B (shown below the flasks), and flasks 3 and 4 correspond to  the -P/+As and -P/-As conditions.

Because I've already found that the cells grow in limiting phosphate without any arsenate,  I expected dense growth (~ 10^9 cells/ml) in flasks 1 & 2 (lots of phosphate), thinner growth in flasks 3 & 4 (limiting phosphate) and even less growth in flasks 5 & 6 (very limiting phosphate).  The graph below shows the results (blue line is initial cell denbsity).  Cultures 1, 3 and 5 grew as expected, but I was surprised to see very little growth in flask 2 and quite thick growth in flask 4 (both with arsenate).  

The most likely explanation was that I'd made a mistake in setting up the flasks - perhaps putting the 1.5 mM PO4 into flask 4 instead of flask 2.

So I set up the cultures again, this time starting them from cells taken from flask 4, because these appeared to have grown well in the presence of arsenate.  (The other cells had been growing without arsenate for about 2 months, and I was worried that they might need time to adjust to this stressor.)  These cultures started with about 10^3 cells/ml.  The graph below shows interim results after only 14 hr incubation; again the blue line is the initial cell density.

All of the cultures without arsenate have grown well; none have run out of phosphate yet.  But there hasn't been any growth in the cultures with 40 mM arsenate; instead most of the cells have died.  These numbers are the density of the cultures yesterday morning.  This morning cultures 1 & 3 were turbid, as expected, but all the arsenate cultures looked clear.

Because these arsenate  cultures looked unexpectedly thin yesterday, I set up another replicate set of 6, using phosphate-depleted cells from the freezer.  I'll have results from these tomorrow, along with the final results from the above cultures.*

So maybe I'll need to gradually re-accustom GFAJ-1 to growing in high arsenate, by first growing them in a lower concentration.  This will take some time, and will have to wait until I get back from Science Foo Camp next Sunday.  I'll also leave the present cultures for another week, to see if cells eventually grow.

Quick check that I made up the sodium arsenate correctly:  The molecular weight of sodium arsenate is 312 (this is the dibasic, heptahydrate version = Na2HAsO4 7H2O), so I put 31.2 g into 100 ml final volume, to give a 1.0 M solution.  I then added 400 µl of this to each 10 ml culture to give 40 mM.

*Tantalizing note added Aug. 8:  Well, my third set of cultures are behaving like the first set - the cells in 3 µM PO4 + 40 mM AsO4 have grown up slightly more dense than the cells in 3 µM PO4 (no AsO4), but the cells with more and with less phosphate haven't grown much at all.  So I probably didn't make a mistake with the first set after all.  I don't know what this could mean, but it is sort-of consistent with the -P/+As and -P/-As results in the Wolfe-Simon et al. figure above...  Unfortunately we'll all have to wait until next week for me to do any more investigating.

A Haemophilus transformation experiment

In addition to my GFAJ-1 arsenic experiments, I'm also doing work on our real research program, natural transformation in Haemophilus influenzae.  We need to (yet again) revise our DNA uptake grant proposal for the Sept. 15 deadline, and I'm doing some work that will let us strengthen that proposal.

The previous version of the grant included a substantial section on making marked and unmarked knock-out mutations of all the competence genes, and one of the reviewers sensibly asked if we could also make point-mutation changes to these genes.  This would indeed be very valuable, so we're trying to generate evidence that we can do this.

The biggest obstacle is not making the mutant versions of the genes (the RA can do that easily in E. coli), but identifying the rare H. influenzae cells that have integrated them into their chromosomes.  We'd like to simply transform the mutated DNA fragments into competent cells, but this works very inefficiently when the DNA fragments are short.  Unfortunately, short fragments work best for the mutagenesis steps.

My latest experiment tested the effect of fragment length on transformation efficiency  I used a cloned DNA fragment containing the novR (novobiocin resistance) allele of the gyrB gene.  This is a point mutation, in the middle of a 9.3 kb fragment.  I did three test transformations, each using the same amount of the plasmid.  Test 1 used plasmid DNA cut to release the 9.3 kb fragment intact.  This gave a transformation frequency of 7 x 10^-3, about 10-fold higher than the control transformation using chromosomal DNA from a novR strain.  Cutting the plasmid with restriction enzymes that gave a 4.8 kb novR fragment reduced the transformation frequency only slightly, to 4 x 10^-3, but cutting with enzymes that gave a 2.6 kb fragment reduced it 10,000-fold, to 4 x 10^-7.

Several factors complicate this experiment.  I don't know the plasmid DNA concentration; I think it was about 100 ng/ml, which would be less than saturating.  The plasmid insert contains several uptake sequences, but I don't know their distribution (I could dig this info out).  The digest that gave the 4.8 kb fragment may not have been complete, in which case the true transformation frequency might be lower.  The control transformation frequency was lower than I expected

We can conclude that our mutagenesis experiments should use fragments that are at least 5 kb long.  If this gives a transformation frequency of only 4 x 10^-3 we'll have to do lots of screening (possible but tiresome), but the transformation frequency can probably be increased ten-fold by using more-competent cells and more DNA.

First evidence refuting Wolfe-Simon et al.'s results

I belatedly realized that the data I posted yesterday are quite important, in that they contradict the growth results in Figure 1 of Wolfe-Simon et al.'s paper.

Here's their Fig. 1B (growth curves based on cell counts), annotated with a table of the levels of phosphate and arsenate they found in their media.

Wolfe-Simon et al. used this graph as evidence that the GFAJ-1 bacteria could use arsenic for growth, in place of phosphorus.  They claimed that growth in the 'added AsO4' medium must be due to the cells using arsenic because (1) this -P/+As medium had no added phosphate, and the small amount of phosphate contaminating most batches was insufficient to support this growth and (2) the cells did not grow in the plain medium (-P/-As), to which neither phosphate nor arsenate had been added.

In my blog and in my published Technical Comment I argued that the ~3 µM phosphate contaminating the medium was indeed sufficient to support the observed growth of ~ 2 x 10^7 cells/ml.  The calculation underlying this argument is shown below.  Given the uncertainty in genome size and in the % of cellular P needed for DNA, my new results nicely support this argument - adding 3 µM phosphate to the -P medium supported growth to 1.7 x 10^7 colony-forming units/ml (equal to at least 1.7 x 10^7 cells/ml).

My new results also contradict Wolfe-Simon et al.'s observation that cells could not grow under limiting phosphate if arsenic was not provided.  No arsenic was added to my low-phosphate media, but the cells grew just fine.  I think that GFAJ-1 might have failed to grow in Wolfe-Simon et al.'s batch of -P/-As medium because this batch contained much less phosphate than the other media.  The levels of phosphate contamination they detected (red boxed area above) were very unpredictable (3.7 µM in one batch, <0.3 µM in another, and 7.4 µM in the wash solution), and the Methods don't say that all cultures in this figure were made with the same batch.

I've now set up some new cultures, testing whether the presence of 40 mM arsenate affects growth in media with no added phosphate or with 3 µM or 1.5 mM phosphate.  I hope the sudden introduction of 40 mM isn't too big a shock to the cells; they've been growing without any arsenate for the past two months.

In other progress, the Research Associate has obtained the 16S rRNA sequence of the strain I'm working with.  It exactly matches the sequence of GFAJ-1 in GenBank, so now we're sure these are the right cells.  This confirmation is especially important since the growth properties I'm finding for GFAJ-1 don't match those reported by Wolfe-Simon et al.

Growth of GFAJ-1 under phosphate limitation

Before we can test whether the bacterium GFAJ-1 can really incorporate arsenic into its DNA when phosphorus is scarce but arsenic is abundant, I need to find out how it behaves when phosphorus is scarce and no arsenic is available.  Here are the results.

The first graph shows how dense cultures got when no phosphate was added to the basic growth medium.  I described this experiment in two posts a few days ago (planning, results), but I didn't show the data.  I started the cultures with cells that were either phosphate-replete or phosphate-depleted, and at densities ranging from 10^4 to 10^7 cells per ml.  All of the cultures except the most dense phosphate-replete one ended up at densities of 1-3 x 10^6 cells/ml.  This tells me that, even though I didn't add any phosphate to the basic medium, each ml contained enough phosphate to produce about 2 x 10^6 cells.  This is about ten-fold lower than the growth observed by Wolfe-Simon et al, and so my experiments should use medium with enough phosphate added to produce about 2 x 10^7 cells/ml.

The second graph shows how small amounts of added phosphate increase the cell density.  These cultures all had the same initial cell density (10^4 cells/ml), but they had different amounts of added phosphate.  As before, medium with no added phosphate yielded about 2 x 10^6 cells/ml, and medium with 1500 µM phosphate yielded about 3 x 10^9 cells/ml.  Media with 3 µM phosphate (the concentration of contaminating phosphorus in most of the media used by Wolfe-Simon) gave a cell density just below 2 x 10^7, and 6 µM phosphate gave about 4 x 10^7.  So I think I'll use 4 µM phosphate as my final phosphate-limiting medium.

Yesterday I also (very carefully) made up my 1.0 M stock of sodium arsenate.  I put on all the safety gear I usually eschew (lab coat, gloves, dust mask, full face shield) and moved our top-loading balance into the fume hood so any arsenic dust would be sucked away rather than entering the lab air supply.  (I even put the balance into a plastic bag so no arsenic dust could get into its innards.)  The sodium arsenate turned out to be in the form of granular crystals (like coarse salt or sugar), not fine powder, so dust wasn't a problem.  But when I carefully unscrewed the cap a lot of grains fell out of it (maybe 0.5 g!), so I was really glad to be working in the hood where cleanup was easy.

Now the arsenate solution is sitting on my lab bench, conspicuously labeled POISON.  Beside it sits a big bottle to discard the waste culture medium into  - this will eventually be sent to our chemical waste facility for disposal.  I'll set up another bottle for waste tips and other solids contaminated with significant levels of arsenic.

CSWA field trips: 3. The Athabasca oil sands

(This is a post I started writing in mid-June.  I think my ambitions for it may have been too high, as it's been dragging along ever since.  It's not as well organized as I would like, but if I don't post it now it'll never see the light of day.)

The full-day trip to the Athabasca oil sands was the highlight of the Canadian Science Writers Association meeting, at least for me.  The tour was sponsored by Connacher Oil and Gas Ltd., a relatively small player in the oil sands business.  They flew a dozen of us up to Fort McMurray (about 400 miles from Calgary) in the morning, and took us first to the Oil Sands Discovery Center and then to their Algar drilling site.

Biologists are very concerned about the issues surrounding development of Canada's oil sands petroleum reserves.  The biggest issue is global climate change, but economics and local ecology are big concerns too.

I'll start with a very simple explanation of how fossil fuels come into existence, using a slide I prepared when I was teaching intro biology.  The text at the top of the slide (in italics) is a question posed by a student in the class, asking about the relationship between 'fossils' and 'fossil fuels'. Plants use solar energy to transform carbon dioxide and water into biological molecules (starch, cellulose, lipids etc). When plants (or animals) die the organic matter they contain is usually eaten by other organisms, but sometimes it's inaccessible to or too much for these 'detritus feeders' and instead is buried, where it breaks down very slowly. The oxygen content of the molecules is usually lost. Commonly the hydrogen is lost too (mostly as methane), leaving behind coal, but sometimes the carbon and hydrogen remain together in the hydrocarbon molecules we call oil.

The figure refers to a paper by J. S. Dukes titled Burning buried sunshine: human consumption of ancient solar energy.  I found this an excellent resource for the class. It explains that we're now burning oil a million times faster than the rate at which it was produced. Put another way, for hundreds of millions of years, a tiny fraction of the carbon dioxide that plants temporarily sequestered was buried rather than being immediately recycled. Now we're dumping all that CO2 back into the atmosphere at once (relative to the very long time scale over which it was buried).  So CO2 that was sequestered very slowly from ancient atmospheres is being returned very quickly as we burn fossil fuel, and this CO2 traps solar energy and disrupts climates all around the world.

In principle, there's only so much buried sunshine, and when it's all gone we'll be able to stop worrying about the causes of CO2 rise and just deal with the consequences.  But the consequences look pretty bad, so prevention would be better.  Unfortunately, not only is Canada a big producer of CO2, its oil industry is a big enabler of CO2 production by other countries.  By extracting oil from the massive oil sands deposits, Canadian industry is making more of this buried sunshine available for burning. Worse, the extraction process itself uses a lot of fossil fuel - separating the oil from the sand requires heat in the form of steam heat, usually generated by burning natural gas.

A separate issue is harm to local environments - extracting oil from oil sands is reported to be particularly destructive, both by ripping away the boreal forest that covers the sands and because of toxic products released both at the mine sites and downstream.  Pipelines are another problem - they can disrupt local environments both by their presence and by leaks, and they can block wildlife movement.  Oil from the oil sands is delivered to refineries in Illinois and Oklahoma by the Keystone Pipeline, and there's a big debate about running a new pipeline (Keystone XL) all the way to Port Arthur and Houston on the Gulf of Mexico.  A final issue is simple economics - if the world is running out of oil, wouldn't Canada be wiser to save its reserves to use or sell later, rather than selling them now to the highest bidder?

So, what did we see on the tour, and what did we learn?

The first thing we saw was the town of Fort McMurray - a little frontier town that's grown very big, very fast because of the influx of oil sands money and workers (see graph).  Housing prices are even worse than Vancouver's.

Next we were taken to the Oil Sands Discovery Centre.  I'm pretty sure this slick tourist attraction exists to put a positive spin on the enterprise, but it's very well done and I learned a lot.  We first watched a cheesy film about the history of attempts to make money by extracting oil from the surface-exposed oil sands.  The extraction itself is very easy; the film was followed by a simple demo using a beaker of oil sand and a kettle of hot water.  Just pour hot water onto the sand and stir - the oil (thick black bitumen*) rises to the top and the sand settles to the bottom.  Initial commercialization attempts were stymied by economic problems, both the cost of the extraction and the poor market for bitumen, especially given the widespread availability of cleaner oil from other sources.  But the market for fossil fuels has grown and collossal scale of production has decreased the cost of producing it from the oil sand.

Most of the Discovery Centre exhibits and equipment displays were about the mining techniques used to extract bitumen from oil sands that are close to the surface.  Until recently this surface mining was the only way to recover bitumen, and it's a spectacularly nasty process.  The accessible oil sands sit under 40-60 meters of 'overburden' - a pit-mining term for the beautiful boreal forest/muskeg and underlying clay and sand.  All of this has to be removed to get at the oil-soaked sand, which is scooped up, mixed with hot water, and piped to nearby extraction plants where ~90% of the oil is removed.  The sand then goes back to the place it came from (more or less), and eventually the surface is supposed to be restored to some semblance of its original state.

Not surprisingly, this makes a big mess.  Here's a Google Earth view of the main mining site north of Fort McMurray; you can get an idea of the enormity of the devastation by the tiny size of Fort McMurray itself, at the lower right (a town of 80,000 residents).  Not only is the surface ecosystem destroyed, but the extraction process uses a lot of water from local rivers, and returns contaminated water first into giant tailing 'ponds' (lake-sized) and then into the river system.

Only about 10% of the oil sands are close enough to the surface to be mined.  The rest is about 500 m deep, but new oil drilling technology now makes these accessible using a much less destructive technology called steam-assisted gravity drainage (SAGD, pronounced 'sag-D').  (The drawings below are taken from here and here.)

With SAGD, the bitumen is extracted form the oil sands in situ; the sand stays deep in the ground while the oil is liquefied by steam heat and pumped to the surface.  This requires drilling two parallel channels about 5 m apart (each about a foot across), first down to the base of the oil sands deposit and then horizontally through the sands.  The ability to drill horizonally with high positional accuracy is the technical advance that makes SAGD possible.  Steam is pumped into both channels until the bitumen around and above them begins to liquefy (about 3 months).  The lower channel (green in the figure) is then switched to extraction mode, pumping the liquid mixture of hot water and bitumen out to the extraction facility on the surface, where the bitumen is recovered and the water is cleaned up and reheated for reuse as steam.  This extraction phase can continue for many years (20?), and, if I recall correctly, can remove more than 80% of the oil without disturbing the sands or much of the surface.

Connacher has two SAGD plants, both about 80 km south of Fort McMurray.  They're much smaller than the big surface mining operation above, and much cleaner.  Each consists of a big array of pairs of wells, as shown in the drawing below.  Below that is another Google Earth image; Connacher's Pod One facility is to the left of the road.  Notice how small the footprint is - this image is zoomed in tenfold relative to the surface-mining image above.  We didn't tour Pod One, but the even newer facility called Algar - it's been in place for only a couple of years and so doesn't yet show up in the satellite photos on Google Earth.

Overall we were very impressed by Connacher's SAGD operation.  There are no mine pits or tailings ponds - the only pond we saw was a tiny one that captures surface runoff (rain and snowmelt) from the extraction site so it can be tested for contamination before being released. 

Water use is also low.  More than 95% of the water used for steam is recovered and reused.  The water doesn't come from the surface (lakes, rivers) but from a deep aquifer of brackish water that's not otherwise usable, and this aquifer is so big that the water withdrawal for SAGD is insignificant.  

One measure of efficiency of oil sands harvesting is the steam-to-oil ratio - the ratio of energy input (largely steam to liquefy the oil) to energy recovery as oil. This matters a lot for the economics of SAGD and also for the global warming consequences, but it's hard to find the numbers. Well no, it's easy to find numbers, but they're usually not commensurate (not in the same units). Barrels of water used per barrels of oil? Cubic feet of natural gas burned per barrel of oil?  Tons of CO2 produced per cubic meter of bitumen?  One of the Connacher engineers told me that the energy input (for steam) was about 1/8 of the energy output (as bitumen), but this seems low.

Can the steam-to-oil ratio be improved?  Luckily this is an economic issue as well as an ecological one, so the SAGD operators have made some advances.  One is to pump the steam in at a relatively low pressure.  This allows more of its heat to be transferred to the bitumen, but requires secondary pumps to push (pull?) the oil-water mix back to the surface.  Another advance is to mix the steam with a solvent that helps the bitumen liquefy at a lower temperature, so less steam is needed.  Connacher is testing this in some of its wells, but I don't have any information about the energy inputs associated with the solvent (where does it come from), how efficiently the solvent is recovered with the bitumen, or even what the solvent is.  I suspect this is all proprietary information.  One company reportedly is using butane, which is also a hydrocarbon - I think such a solvent would be neutral with respect to global warming, being either burned directly (in uses unrelated to the oil sands) or recovered with the bitumen and eventually burned. And any solvent that isn't recovered would be a hydrocrarbon that isn't even burned.  So appropriate use of solvents in SAGD would be good for the atmosphere.  Solvents such as butane are less ecologically nasty than the bitumen itself, so any solvent that stays in the ground is unlikely to cause problems.

The disruption to the surface ecosystem is much less than caused by surface mining.  Not only is the area disturbed much smaller (just the main extraction facility, pipelines and access roads), but the disturbances needed are much shallower and thus easier to restore.  Connacher operates under quite strict ecological regulations imposed by the Alberta government, and they appear to take these very seriously.  They monitor wildlife using the same kinds of remote cameras we saw at Banff, although they're strictly forbidden from interacting with any of the wildlife they see. 

I don't know how much of the good impression Connacher made on us was created by high-quality spin.  Our group of science writers felt that we were pretty good at detecting spin, but we could be mistaken.  One ecology colleague of mine, whose paranoia has been honed by years of public service, suggested that the whole Connacher operation might have been created by the giant oil sands companies as a public relations showpiece (a 'Potemkin village'?).  And the cleanliness and efficiency of their operations does nothing to mitigate the global warming consequences of burning buried sunshine.

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* Wikipedia says that bitumen is the correct name for the tar-like crude oil in these sands.  It's a very complex mixture of polycyclic aromatic hydrocarbons - hydrocarbon chains that have been extensively cyclized and crosslinked into viscous tangles.

Simulations run successfully, but drowning in contamination angst

After some futzing around I rediscovered how to run my computer program that simulates the evolution of DNA uptake sequences in genomes.  So now I've done 4 runs, using uptake-bias matrices derived either from our previous genome analysis or from the postdoc's new uptake data.  There are 4 runs because I started each matrix with either a random 20 kb DNA sequence or a random 20 kb DNA sequence pre-seeded with 100 uptake sequences.

Now I've just sent the input and evolved sequences to the postdoc - he will analyze them with his new uptake-sequence-prediction model and with the old-genome-derived model.  We hope this will help us understand why our previous view of uptake specificity was wrong.

He and I have spent months (and months and months) working on the manuscript that describes his DNA uptake results.  Lately I've been griping that he's too much of a perfectionist, always trying to make sure the data and analysis is absolutely perfect rather than just getting the damn manuscript written and submitted.  But I've now fallen into the same trap, spending days trying to understand exactly how contamination of one DNA pool with another might be compromising his analysis.  (The Excel screenshot below is just for illustration - there's lots more data where that came from.)  And it's not the first time I've been the one to insist on perfection - last month I spent weeks making sure we really understood the impact of sequencing error.

But we also have a reason to celebrate, as his paper on recombination tracts just appeared in PLoS Pathogens:  Mell, Shumilina, Hall and Redfield,  2011.  Transformation of natural genetic variation into Haemophilus influenzae genomes.  Open access, of course.

RRResearch: Phosphate levels and DNA controls for GFAJ-1

OK, it looks like my arsenic-bacteria experiments have advanced from "Why won't they grow" troubleshooting to real science.  My test of growth in medium with no added phosphorus (P- medium) succeeded nicely.  All of the cultures except the most dense grew to the same low density of about 4 x 10^6 cells/ml.  This tells me that their growth was indeed limited by the small amount of phosphorus contaminating the medium.  It also tells me that my P- medium contains less phorphate than the medium used by Wolfe-Simon et al., as the cells grew to about 2 x 10^7 in their P- medium.  This means that I should add a small amount of phosphate (~ 3 µM) to my P- medium to replicate the growth conditions they used.  I'll set up cultures with this medium tonight to check that growth is as expected.

I've also been thinking about controls for the DNA purification steps.  This weekend I'm going to make up my arsenic solution (100 ml of 1.0 M Na2HAsO4).  A colleague has given me her procedure for safely weighing out the powder in the fume hood (that's the only seriously risky step).

To check that my DNA-purification procedure does get rid of free arsenate from the medium, I'm going to do the following:  I'll start with about 1 mg of old H. influenzae chromosomal DNA that we no longer need for other experiments.  I'll mix it with some AML60 medium containing 40 mM arsenate, and then put it through the purification steps I plan to use on the GFAJ-1 DNA - two rounds of ethanol precipitation with the DNA collected by spooling, and a final spin-column purification.

I'll save a sample of the DNA after each step, and send all the steps to my collaborators for mass-spectrometry analysis of its arsenic content.  Ideally the DNA will not contain any detectable arsenic.  If it does, I can try more extensive purification, or just accept this level as the baseline, depending on how sensitive the mass-spec turns out to be.

Once I have the growth results from my medium with 3 µM phosphate, I'll also use my new sodium arsenate stock to make some 3 µM P medium that also has 40 mM arsenate, and then test whether the arsenate inhibits growth at all, or whether it enhances it as reported by Wolfe-Simon et al.  Then I can grow a big batch of cells in 3 µM P 40 mM As, purify DNA, and send the DNA to my collaborators for analysis.

And the Research Associate has already amplified the 16S-rRNA gene from the GFAJ-1 DNA I made and sent it off for sequencing (she's a whiz!).  So next week we'll be certain that I'm working with the right strain.  Or not.

Simulating evolution of uptake sequences with our new uptake-bias matrix

One of the things the post-doc and I want to do with his new DNA uptake data is test what how it behaves with our old perl simulation of the evolution of genomic uptake sequences.

This analysis is prompted by the disparity (dissonance? discrepancy? disagreement?) between the uptake bias he's measured with his degenerate DNA fragments and the sequences overrepresented in the genome.  The top part of the figure is a diagram of one of the DNA sequences that H. influenzae cells prefer to take up.  The middle part is a 'sequence logo' based on the related sequences found in the H. influenzae genome, and the bottom part is a logo based on the uptake biases measured by the post-doc.

Because the two logos were drawn from very different datasets, we can't directly compare their overall 'importance' (the technical term is 'information content', indicated by the height of each column of letters); I've instead just shrunk the height of the genomic logo image so its overall importance appears similar to that of the uptake logo.  

The two logos still look very different, even though their consensus sequences are both identical to that shown on the double helix above them.  The genome logo has a block of nine 'core' bases on the left, all of roughly equal importance (indicated by their height, and two 'T-tracts' on the right.  But the core bases in the DNA-uptake logo have very different importances, with four (GCGG) being much more important than the others.  The T-tracts in the uptake logo also appear much less important than those in the genomic logo.

We think the sequences in the genome accumulated (over many millions of years) due to the sequence bias of the cells' DNA-uptake machinery, so we don't understand why the two patterns are so different.  Maybe other cellular processes contribute additional sequence biases, or maybe the difference is just an artefact of the way the genome sequences were identified.  One way to (maybe) clarify the issues is to simulate the accumulation process in a computer program.  We already have such a program (described in this research paper), and have used it with the data matrix that specifies the genomic logo.  So in principle all we need to do is run this program with the new uptake-based matrix.

In practice, not so easy.  The model is quite complicated even though the processes it simulates are treated very simply, and I've forgotten all the details about how it works.  Luckily it's quite well documented, and the paper describing it is very clearly written (I'm patting myself on the back for this).  One thing I do remember is that the program ran very slowly when dealing with the big genomic matrix (29 positions) rather than the short fake matrix we used for most runs.  I can help it out by specifying a fast mutation rate, a short genome and short DNA fragments, and by seeding the genome with some partial matches to the uptake sequence consensus.

Migrating isn't the best word for what's happening to this blog...

It's certainly not moving with the herd, or flock.  Emigrating maybe (leaving one population and joining another)?  The blog's home is moving from Blogger to Field of Science, a much more select and congenial environment.

For regular readers, nothing much should change, though I hope the pages will get better-looking.

For new readers I should explain what happens here.  I run a small research lab at the University of British Columbia; our lab home page is here.  As the blog header says (yes, it's too brusque and unfriendly; it'll change too), here I mainly write about the research that I and the members of my lab are doing, day to day.  This gives readers a slightly-sanitized window into the real research experience (best described as "Most scientists spend most of their time trying to figure out why their experiments won't work.").  I try to provide a bit of background to the experiments, but unless you're a regular reader you probably should just view these posts as brief glimpses of a scientist's thinking style.

Sometimes I also write about other ideas, or critique published research papers from other labs.  One such critique, of the NASA-sponsored research paper claiming that bacteria can put arsenic into their DNA in place of phosphorus, led to one of my current projects - testing that claim.  So far I've spent most of my time trying to figure out why the cells won't grow.

Now back to regular posting...

Growth of GFAJ-1 under phosphate limitation

Before I can properly test whether GFAJ-1 cells put arsenic into their DNA backbone when they're starved for phosphorus, I need to carefully characterize how phosphorus starvation affects their growth in the absence of arsenic.

Yesterday I inoculated medium that had no added phosphate with cells that had been growing in medium with 1.5 mM phosphate. I'll call the no-added-phosphate medium 'P- medium', even though it likely contains a low concentration of contaminating phosphate, and I'll call the cells grown in P+ medium 'P-replete' cells. The cells doubled 3-4 times before growth stalled, reaching a density of about 2 x 10^8 cells per ml.  I'll call these cells 'P-depleted' cells; I froze about 15 vials of them to use for starting future phosphate-limited cultures.

Some of this growth was no doubt due to the contaminating phosphate in the -P medium, but I suspect that most of it was possible because the cells contained quite a lot of non-essential phosphate, mainly in the form of ribosomal RNA. Today I started another experiment to tease apart the effects of P in the medium and in the P-replete cells.

I inoculated P- medium with P-replete or P-depleted cells, at initial densities of 10^4, 10^5, 10^6 and 10^7 cells/ml.

As diagramed in the graph below, I expect the low-density cultures of P-depleted cells (dashed lines) to all grow to the same low final density, all limited by the low level of P contaminating the P- medium.  I expect the high-density cultures of P-replete cells (solid lines) to all increase in density by the same factor, all limited by the relatively large amounts of P present in each P-replete cell.

Although the graph doesn't show this, I expect the lowest density cultures of P-replete cells to reach only the same low density as the P-depleted cells.  And the highest-density culture of P-depleted cells might grow to a higher density that the others, depending or how low the P contamination is and how depleted of P the cells are.

Next steps

Now that I have good growth conditions for GFAJ-1, I need to plan the rest of the work in more detail.

Frozen cell stocks:  I'll want to start my phosphate-limited cultures with cells that have been pre-grown under phosphate-limited conditions, so that their subsequent growth will be limited by the phosphate in the medium, rather than by the phosphorus they have accumulated in RNA and other molecules.  I have about 50 ml of dense culture in +P medium, so I'll wash these cells, resuspend them in a large volume of -P medium, and incubate them just until growth stalls**.  To make monitoring easy I'll start the cultre at the final OD reached by my original -P culture; at this density I expect the cells to run out of phosphate within a few doublings.

(** I need to be careful that apparent cell density isn't being influenced by accumulation of poly-hydroxybutyrate, as it was in the Wolfe-Simon paper.  So I'll also plate the cells to check that numbers are no longer increasing.)

Once I have a phosphate-limited culture I'll collect the cells (by filtration or centrifugation), resuspend them at high density, and freeze 1 ml aliquots of them in 15% glycerol.  I'll check the cell density by plating before and after freezing, to make sure that freezing doesn't kill the cells.

DNA prep:  I should have enough cells to also make my first DNA prep - if not I'll inoculate one of my freezer-stock tubes into a new overnight culture.  I'll put this DNA through the same multiple purification steps I plan to use for DNA from arsenic-grown cells, checking the DNA concentration at each step, and running a gel to confirm the quality of the DNA and the absence of contaminating RNA.  This will let me estimate the loss in each purification step, so I'll know how many cells I'll need for the arsenic-grown DNA prep.

Elemental analysis:  I'll send aliquots of the media and some of the DNA to my collaborators, so they can check levels of phosphorus and arsenic.  We can consider this to be our control DNA - if the DNA from arsenic-grown cells has no more arsenic than this DNA, we can conclude that arsenic-grown cells do not put arsenic into their DNA.  It will be good to test this DNA now, as it sets the limit of detection we need for the arsenic-grown DNA.

However, when I purify the DNA from the arsenic-grown cells I'll also do a second control, by briefly incubating phosphate-grown cells in the arsenic medium before DNA purification.  This will control for any carryover of arsenic in the DNA purification.  If my purification is adequate I expect this DNA to have no more arsenic than the first control.

Strain identification:  I'll give some of the DNA to the RA.  She has the primers for the 16S rDNA amplification and will get it sequenced to confirm that these bacteria are GFAJ-1.

Hmm, did I do this experiment 20 years ago?

Today at lab meeting we discussed our plans for creating specific point mutations in competence genes.  This is something that one of the reviewers of our CIHR proposal wanted to see, and we think we can do it before the next grant deadline (Sept. 15).

The RA has a clever way to make any desired point mutation in our cloned competence genes, and we can easily introduce such mutations into the H. influenzae chromosome by natural transformation.  The big problem is getting a high enough transformation frequency that we can identify the desired mutants by PCR.  Because the mutations don't have an associated antibiotic resistance we won't be able to select for them, and because we won't usually know the effect of the mutation in advance we may not be able to screen for an expected phenotype.

We know that transformation frequency depends on the length of the fragment, the kind of heterology (single nt, insertion/deletion, etc), and the presence of uptake sequences.

We want to do some preliminary experiments to check the effect of fragment length.  In the past I had gotten transformation frequencies of better than 5% with a 9 kb restriction fragment containing a cloned novobiocin-resistance point mutation, but more recent experiments with shorter fragments had given frequencies that were 100-fold to 1000-fold lower.  So we were planning to do a new test, first cutting this novR fragment to different lengths with restriction enzymes and then measuring the effect on transformation frequency.

But while looking up the restriction map of this plasmid I discovered that I and my first technician had done a version of this experiment already, back when we were first working with this plasmid (RR#196).  I think we weren't testing how fragment size affects transformation, but just finding out whether we should cut the insert free of the vector.

The plasmid has a 9.25 kb fragment of chromosomal DNA in a 2.3 kb pSU vector; the novR mutation is somewhere in the 2.4 kb gyrB gene (the postdoc knows where but he's not here right now).

The technician's transformation frequency results:  Using an uncut plasmid: 0.024; linearizing the plasmid, leaving the vector attached to the insert: 0.061 and 0.086; cutting the insert free of the vector: 0.093; cutting the plasmid once, about 2 kb from one end of gyrB: 0.051; cutting the plasmid once, 70 bp from one end of gyrB: 0.036.  (One time, I got a transformation frequency of 0.22 with this DNA!)  Transformations that used the same novR marker carried in chromosomal DNA gave a transformation frequency of 0.011.

These are lovely high transformation frequencies - if we can get similar frequencies with our engineered mutants we'll have no trouble identifying them by PCR.  Another limiting factor is how much DNA we can use.  I don't have a good estimate of the DNA concentration the technician used in this experiment, but in a later experiment (RR#860) I used 100 ng of insert, from plasmid grown in either H. influenzae or E. coli, and got transformation frequencies of 0.045 and 0.07 respectively.  So if the RA can generate 100 ng of mutant fragments (perhaps by long PCR) then we'll be all set.

But generating long fragments is a pain, so we still need to test the efficiencies of transformation with shorter novR fragments to find out how long her fragments need to be.  This means that we need to grow up a prep of the plasmid.  I've had problems with yield of this plasmid in the past (it's a low-copy vector), but the post-doc is confident he can get lots, so I'm streaking the strain out for him now.  If yields suck we can always reclone the insert in a high-copy vector.

We are not alone!

I've just been exchanging emails with someone else who is trying to grow GFAJ-1 "to look at the DNA".  They're also dealing with a media-related problem, though not the same problem as mine.

Growth properties of GFAJ-1's relatives?

To help me figure out what nutrient might be missing from the AML60 medium I'm trying to grow GFAJ-1 in, I'm reading about its Halomonas relatives.

Here's a tree showing the relationship between GFAJ-1 and its closest known relatives (source).

And here's a link to a paper describing VERY THOROUGH phenotypic characterization of all the formally described species of Halomonas:  Mata et al., 2002.  A detailed phenotypic characterization of the type strains of Halomonas species.  System. Appl. Microbiol. 25:360-375.  I was initially assuming that GFAJ-1 would be quite picky about growth conditions, but if it's a typical Halomonas species it's probably quite robust, as they all tolerate wide ranges of salt concentration, pH and temperature.

They're growing...

Two nice preliminary results:

First, GFAJ-1 cells grow well in liquid AML60 medium supplemented with 10 mM glutamate.

Second, they don't grow much at all if I omit the phosphate from the AML60 medium.

Together this means that I now have conditions for investigating whether the cells can incorporate arsenic into their DNA when phosphate is limiting.

But I first need to now do some careful growth curves.  This will be relatively easy because I've realized that Halomonas are nutritionally quite versatile, and I can get good colonies on agar plates overnight if I supplement the AML60 medium with tryptone or yeast extract.

(still no tungsten...)

Email to my GFAJ-1 collaborators

Hi Leonid, Josh and Marshall,

If you've been checking my blog you'll know that I'm still fussing around with growth conditions for GFAJ-1.  Before doing any more work I want to check with you to make sure we agree that it's worth proceeding.  (I'm off at a Gordon Conference this week.  Various batches of cells are in the incubator, so I may have more growth results when I get back.)

Basically, I haven't observed cell growth in the liquid version of the AML60 medium described by Wolfe-Simon et al.; instead the cells just very slowly die.  But the cells grow very well when this medium is solidified with agar.  They don't grow if it's solidified with agarose, so I think the agar is providing a missing nutrient.  The cells grow very well in liquid AML60 if I supplement it with Casamino Acids (hydrolysed casein) or with an amino acid mixture we use in our competence induction medium.  Neither of these supplements can be used in my growth experiments because they contain too much phosphate, so I'm going to test addition of individual amino acids - initially just glutamate and aspartate since they're what's in our competence mix.

An additional complication is that my version of AML60 medium is still not exactly what Wolfe-Simon et al. described:  First, the trace element mix I'm using doesn't contain tungsten (Oremland's lab adds 45 nM sodium tungstate to their minimal media, but there's no evidence that GFAJ-1 needs this); I've ordered some, and I'll add it when I get back.  Second, I realized that their version of the basic AML60 salts lacked potassium, so I'm adding 10 mM KCl to my medium.

I'm confident that I can find a suitable growth condition for the ±P/±As growth experiments.  But this probably won't be exactly the same condition reported by Wolfe-Simon et al., so we need to decide whether it's appropriate to use my growth condition to test their observation.

Here's what I would do:

1. Test growth on medium with and without each of my candidate supplements (single amino acids), with and without added phosphate.  (At present all my media have 1.5 mM phosphate added.)  I want to see that cells grow to high density with at least one of the supplements, but only when phosphate is provided.  (If they grow well without any supplement, that's even better.) 
2. Choose the supplement that gives the fastest growth or the highest growth yield.  Do careful growth curves with and without the supplement, with and without 1.5 mM phosphate.  Perhaps test intermediate phosphate levels too (3 µM and 30 µM?), since I don't know how much contaminating phosphate my medium might contain.  I would monitor growth by plating dilutions on supplemented AML60 agar, and perhaps by flow cytometry (the flow-cytometer person might not be willing to count cells in 40mM arsenic), as microscopic counting turns out to be a pain in the butt.  The goal is to get publishable data (1) showing that the cells won't grow in the specified medium, and (2) establishing suitable phosphate-limited growth conditions for the arsenic test.  If the cells don't grow at all in supplemented medium with no added phosphate I'll use medium with 3 µM phosphate added.
3. Prepare DNA from the phosphate-replete and phosphate-limited cultures.  Use PCR and sequencing to check that the strain I'm using really is GFAJ-1.  Send you samples of the DNA and the culture media, so you can confirm that your mass-spec assays will work.  You have yet to tell me how much DNA you will need; to get enough DNA I might need to grow a scaled-up version of the phosphate-limited culture.
4. Again grow cells in the supplemented AML60 medium, phosphate-replete and phosphate-limited, this time with and without 40 mM sodium arsenate added to the media.
5. Grow a scaled-up culture of the cells in 40 mM arsenate plus limited phosphate, and prepare DNA.  Send you samples of the media and the DNA.

The test of arsenic incorporation into DNA will thus be done in slightly different medium than that described by Wolfe-Simon et al.  I expect the cells will also grow much faster in this medium, since on agar plates or with my crude supplements they double every 3 hr rather than the every 12 hr seen in Wolfe-Simon et al.'s Fig. 1B.

Do you think that this would be seen as a valid test of the reported result?  If not I'll probably stop now, as I have lots of other work to do.

Rosie

Do bacteria communicate using nanotubes?

Until Friday I'm at the Microbial Population Genetics Gordon Conference, a black hole from which no tweets or blog posts must emerge.  Well, that's an exaggeration - we just can't tweet or post about the conference.  But someone at last night's excellent poster session drew my attention to a remarkable paper published in February, and now that I've read it I'm going to write about it here.

The paper is titled Intercellular nanotubes mediate bacterial communication.  It's by Gyanendra Dubey and Sigal Ben-Yehuda (Hebrew University) and appeared in Cell 144:590-600.  (It's behind a paywall here, but you can find a pdf of it here at OpenWetWare).The authors found that Bacillus subtilis cells form tubular connections through which small molecules, proteins and plasmids can pass from one cell to another.  Although the authors' ideas about bacterial communication and cooperation appear to owe more to Sesame Street than to evolutionary theory, this is a very surprising and important finding.

The paper first reports that, when a mixture of B. subtilis cells with and without GFP were mixed on an agar-solidified medium,  GFP- cells lying next to GFP+ cells gradually acquired GFP.  The same transfer happened if some cells instead were preloaded with a different fluorophore, one known to not pass through cell membranes.  If the cells contained different chromosomally encoded antibiotic resistance proteins, some cells became transiently resistant to both antibiotics.  And if some cells contained an antibiotic-resistance gene on a plasmid, some of the plasmid-free cells acquired the plasmid.  Plasmid acquisition was not blocked by DNase I and did not occur when a sub-inhibitory concentration of the detergent SDS was added to the mixed cells or when free plasmid DNA was added to plasmid-free cells.

The obvious next step was to look at the cells with electron microscopy.  This showed tubular connections between cells, which the authors unfortunately chose to call 'nanotubes'.  (Unfortunately because nanotube is a very well established term for tubular filaments of fullerene

How the authors prepared the cells for EM is probably important.  Normally cells are first suspended in liquid and then placed on an EM grid, but this might disrupt any cell connections.  So instead the authors grew cells on agar medium for 3 hr, and then placed EM grids on top of the cells.  They let the cells grow for 3 more hr and then lifted the grids and the attached cells from the agar.  It would have been good to have repeated this unconventional procedure using cells that were already dead when placed on the plate, or otherwise incapacitated so they couldn't actively form connections.  This would show that the apparent connections aren't just coming from the agar. 

What's bizarre about this result is that nobody has ever observed these connections before, but the authors don't discuss why the connections wouldn't have been discovered by earlier B. subtilis researchers. It's true that researchers may not have used exactly these conditions.  However the connections must have formed quite quickly in their experiments, as evidence of transfer was seen within 15 minutes, so I would think that anyone looking at cell behaviour under a microscope would have noticed that cells became stuck together. 

It could be that microbiologists have overlooked this because bacteria aren't usually co-cultivated or agar surfaces.  But growth on surfaces is the norm for bacteria in natural environments.  If connecting tubes and molecular transfer were this ubiquitous, phages and plasmids would be much more uniformly distributed both within and between species.  Evolutionary processes would also be very different; mutant phenotypes would blend when different strains made contact.

Overall I'm dubious. The data looks OK, but the phenomenon doesn't make biological or evolutionary sense.

***A few more details I picked up on rereading the paper:

• The frequency of plasmid transfer after >4 hr of co-cultivation was only 10^-7.  That's very low, given the apparently high transfer rate of other molecules.
• Transfer was blocked by levels of SDS that didn't affect cell growth - this suggests that the tubes do not have the same envelope as the cell bodies.

On other research fronts...

The postdoc and I continue to work on his DNA uptake specificity manuscript, temporarily distracted by (1) the need to prepare a poster for the Gordon Conference on Microbial Population Biology, which I'll be attending next week (no tweets or live-blogging, by conference policy); and (2) the belated arrival of the sequencing output for the 88 recombinant clones he submitted to the Genome Sciences Centre 8 months ago.

I've also repeated the controls for my phage recombination experiments.  This time they worked well, and I realized that 'infectious centers' are not a good way to estimate recombination.

The Research Associate has me doing competence assays on the collection of knockout mutants she's generating.  I can do these much more efficiently than anyone else in the lab - I've done 12 in the past week.

Two mistakes discovered

My GFAJ-1 cells grow on the designated medium (AML60) if it is solidified by agar, but not if it is solidified with agarose.  In response to a tweet I sent out about possible nutrient differences between agar and agarose, Mark Martin suggested potassium.  This led me to the discovery of two errors, one by me and one by Wolfe-Simon et al.

My error was that my stock phosphate solution was sodium phosphate, not potassium phosphate as specified by Wolfe-Simon et al.  Because the specified no-phosphate AML60 base recipe does not include a source of potassium, my liquid medium had no potassium.  Agar does contain potassium as a contaminant; the analysis of Bacto agar lists 0.121% potassium.  My back-of-the-envelope (literally) calculation converts this to about 0.2 mM potassium in medium solidified with 1.5% agar.  That's not a lot. but probably enough, and tenfold more than is present in agarose.

Wolfe-Simon et al's error makes their growth results even harder to interpret.  The originally published recipe for AML60 medium ('artificial Mono Lake') includes 1.5 mM potassium phosphate, which provides both potassium and phosphate.  (The lake water is about 24 mM potassium.)  This medium was modified by Wolfe-Simon et al, who initially removed the phosphate and replaced it with arsenate.  Although they used potassium phosphate for their +P version, they used sodium arsenate, not potassium arsenate, for their +As versions. Thus their arsenate-grown cells were starved for both arsenate and potassium.

Anyway, I've now added 2.5 mM potassium chloride to my AML60 medium.

Life and death of GFAJ-1

Because the GFAJ-1 cells have been growing well on plates (visible colonies in less than 48 hr), I've started using colony counts to follow their growth (or lack of it).  Two little experiments highlight the problem.

First, I tested the growth of cells in several tiny colonies that had grown up in 48 hr on agar plates with the complete ML60 medium.  I sucked each colony up into a micropipette tip and resuspended it in 100 µl of ML60.  Then I spotted 1 µl, 10 µl and the remaining 89 µl onto a new agar plate and incubated it for 48 hr.  The 1 µl spots each produced more than a thousand new colonies, which means that the original colonies each had more than 10^5 cells.  This means that, on agar plates, the cells are doubling in less than 3 hours, much faster than their fastest doubling rate seen in Fig. 1 B of the Wolfe-Simon et al. paper (~12 hr).

Second, I tested the growth of cells in liquid ML60 medium.  I had a stock of cells that had been grown in a layer of liquid ML60 overlying the surface of a ML60 agar plate.  I serially diluted these cells in liquid ML60 (10^-1, 10^-2 ... 10^-6), and spotted 10 µl of each dilution onto agar plates.  After 48 hr the 10^-5 dilution had produced about 50 colonies, indicating that the original stock had about 5 x 10^8 viable cells per ml.  While the agar plates were incubating I also incubated the dilutions I'd made, and after 48 hr I plated them again.  Now the 10^-5 dilution spots produced only ~1 colony, and the 10^-4 spots produced ~15.  This means that 95% of the cells had died in the same medium that, when solidified with agar, they grew very well on!

Today I'm going to several more tests:

First, I'm going to make a completely new batch of the ML60 medium base, and test whether cells grow better in it.

I've already tested whether cells grow better sealed in screw-cap glass tubes (used by Wolfe-Simon et al.) rather than in loosely capped glass tubes - they don't.  using the sealed tubes lets me test whether they grow better when gently agitated.  I can't fit a roller wheel into my little 28°C incubator but I can fit a rocker platform.  But I first needed to test whether the rocker motor produced too much heat, as this would raise the temperature of the incubator above 28°C.  The temperature seemed OK last night, so they cells in sealed tubes have been rocking overnight.

Finally, I'm going to test whether GFAJ-1 cells use agar as a carbon source, by plating them on agar-solidified ML60 with no glucose, and by adding agar rather than glucose to the liquid medium.  Maybe I'll also test whether they grow on ML60 solidified with agarose (much more pure than agar).  I don't think that we have any gellan (an agar substitute), but I know that a lab upstairs does, so I might test that too.

The big question is, should we still try to test whether GFAJ-1 put arsenic in their DNA, if I can't grow them under exactly the conditions that Wolfe-Simon et al. used?  

Howard Gest says that 'astrobiology' is an oxymoron

Howard Gest, Emeritus Professor at Indiana, has posted an article about astrobiology on his university's document server.

The title says it all:

On the Origin, Evolution, and Demise of an Oxymoron: “astrobiology.” 

A Select Time Line, from Elephants on the Moon to Phantom Microbes on Mars, onto Earth’s Bacteria in the Guise of Extraterrestrial Life and the Arsenic Monster of Mono Lake. 

Touching on: astrobiology follies, bacteria, chicken pie, exobiology, extremophiles, fossil microbes, Mars, media mayhem, meteorites, moon dust, NASA, phantom microbes, War of the Worlds, and sundry other topics.

I especially like his dig at those physicists who assume that all the major problems in biology can be solved by the application of a little physics-derived common sense:

Why is it that biologists never advance hypotheses on problems of physics relating to quarks, gluons, black holes etc., whereas many physical scientists (physicists, astronomers, geologists etc.) have attempted to explain major complex unsolved problems of biology? 

More phage recombination work

I finally found some time to do more phage recombination work.  I still need to repeat the experiment showing that DNase I pretreatment of lysates reduces phage recombination but not phage titer) and that protease pretreatment reduces phage titer but not phage recombination.  But this experiment was instead testing whether phage recombination is affected by mutations that eliminate DNA uptake or reduce chromosomal transformation.

Each test involves infecting cells with amixture of two temperature-sensitive phage mutants (ts1 and ts3), and plating the progeny phage at the restrictive temperature of 41 °C.  I tested two uptake-null mutants, pilA and rec2.  rec2 mutants are known to be defective for phage recombination; pilA has never been tested but I expected the same phenotype, based on the hypothesis that phage recombination depends on uptake of phage DNA by the competence machinery.  I also tested knockouts of three cytoplasmic-protein genes in the competence regulon, dprA, comM, and radC. 

As positive controls I tested phage recombination in competent wildtype cells, and phage production using wildtype phage.  As negative controls I tested phage recombination in log-phase wildtype cells (no recombination expected), and infection of wildtype cells with each phage mutant singly (no plaques expected at the restrictive temperature).

The positive control infection gave a recombinant frequency of 5 x 10^-3, as expected, and the single-infection controls worked well - no plaques at 41 °C, giving revertant frequencies of <3 x 10^-6 (ts1) and 3 x 10^-5 (ts3).  But the negative phage-recombination control (log-phase cells) and the known recombination-negative mutant (rec2) both gave way more plaques at 41°C than expected (frequencies of 2 x 10^-4 and 9 x 10^-5 respectively). 

Three of the previously untested mutants had recombination frequencies similar to the negative controls (pilA: 1.6 x 10^-4; dprA: 1.3 x 10^-4; comM: 2.7 x 10^-4), and the radC mutant, which has normal frequency of chromosomal transformation, had a near-normal frequency of phage recombination (1.2 x 10^-3).  But these values are not very useful because of the high background.  Need to do it again.

GFAJ-1 (no real progress to report)

I'm now using the medium exactly as specified, but the cells still aren't growing consistently.  They also form variable numbers and sizes of Tween 20-resistant clumps.

More detailed plans

1. Get the GFAJ-1 cells growing in liquid ML60 medium (with vitamins and trace elements) at least as well as they grew for Wolfe-Simon et al.  That means at least two doublings a day.
2. Do preliminary growth curves to find out what phosphate concentrations limit growth.
3. Grow a big batch of cells under phosphate-limiting conditions.  Collect them and freeze them when they are still growing exponentially (so no complications due to accumulation of poly-hydroxybutyrate granules).
4. Do meticulous growth curves with different concentrations of added phosphate with and without 40 mM arsenate.  Also try media with no added phosphate, in case my phosphate-contamination levels are like those in the paper.
5. Grow enough cells at the lowest phosphate level, with and without arsenate, that I can purify enough DNA for analysis.  
6.  Send the DNA and samples of the various media to Leonid Krugliak and Josh Rabinowitz, who will use mass spectrometry to measure phosphorus and arsenic levels.  I'm waiting for them to tell me the sample sizes they'll need.

I think I should also do a preliminary DNA prep soon, just to check how much DNA I get and how much is lost during the purification steps.

I'll also ask the RA to order the universal 16S rDNA primers so we can use PCR and DNA sequencing to confirm that the cells I'm growing are indeed GFAJ-1.