Do competent cells stick to an agar layer containing DNA?

Apparently not.

I made plates of agar culture medium topped with a thin layer of agar containing chromosomal DNA (1 µg/ml or 10 µg/ml).  I layered ~ 10^8 cells (log phase or competent) on top of the DNA-agar, let them sit for 10 min, and then washed the surface by flowing buffer over it (2 x 25 ml).  Then I overlaid the agar with 1 ml  of medium ± DNase I.  Finally I washed the agar surface one last time with 25 ml of buffer and plated both this final wash and the top agar itself. 

If the competent cells were able to bind to the DNA I had mixed into the top agar, I expected to see many more competent cells than log-phase cells in the top agar when DNase I wasn't used.  And when DNase I was used, I expected Wash 3 to contain most of the cells that would otherwise be with the top agar.  But neither of these effects were seen.

I don't know if the differences between the log-phase cells and the competent cells (leftmost bars vs all the other bars) are significant.  It could just be because the log cells were my first attempt.

But there are clearly no significant differences caused by treatment with DNase I, nor by use of the two different DNA concentrations.

Controls I failed to do: 

• Top agar with no DNA.  This would control for non-specific sticking.
• Transformation of the cells by the NovR allele in the DNA.  If this gives no transformants, maybe none of the DNA was exposed above the agar surface.  If it gives lots of transformants, maybe the exposed DNA was all released from the agar into the medium.

Other changes I could try:  There's no reason to put the DNA-agar on top of normal sBHI agar, since I'm not going to try to grow the cells.  Instead I can just make thin layers of agarose with DNA, varying both the agarose concentration and the DNA concentration.  I could try higher DNA concentrations, up to 100 µg/ml.  For ease of washing I could make these on glass slides rather than in Petri dishes.  (Nope - just tried that and the agar just slid off the slide when I washed water over it.)

Tangled up in goo?

I just reread an opinion piece from Richard Moxon's group, considering whether H. influenzae produces anything that should really be called a biofilm.  They agree that H. influenzae cells will grow on surfaces, but they don't think there's any real evidence that these films are the result of a developmental program that evolved because of the benefits of biofilm formation.

Although 'biofilm' can simply mean a layer of bacterial cells and biological macromolecules, associated with a solid surface or an interface, most microbiologists assume that  biofilms arise by regulated developmental programs.  Said another way, most microbiologists think that bacteria grow in biofilms because natural selection has favoured genes that cause them to do so.  They think that bacteria respond to certain stresses that arise in biofilms, or simply to the presence of a surface, by turning on sets of genes that optimize their ability to initiate a biofilm and the physical properties of the biofilm that forms.

It's not that researchers have rigorously evaluated and discarded the alternative explanation - that biofilms form just because bacteria have adhesive organelles and macromolecules are often sticky and fibrous.  But they, and grant agencies and journal editors, find the adaptive perspective more interesting, so that's what gets done and published.  The Moxon paper is complaining that the term biofilm, with its aura of scientific coolness, is being applied to H. influenzae structures that fit only my simple non-adaptive definition.

Thus at least part of the reason why my simple DNA-on-glass-tubes experiment didn't work is probably that the H. influenzae cells were never going to form a biofilm at all.

After we discussed this at lab meeting, I'm going to try something different.  I'll make a fake biofilm by putting a layer of top agar that contains DNA on top of normal agar plates, and then testing whether cells stick to the surface.  I'll also return to an experiment I did by accident when I was a post-doc, which showed that multiple cells can bind to single DNA fragments in solution.

Nothing to see here folks

My repeat biofilm experiment was seriously compromised by a tube-label failure - the identifying numbers I'd written on the culture tubes mostly washed off when I washed the crystal violet stain from the tubes. (Somehow my new red sharpie's writing didn't stick to the surface of the new glass tubes, but instead flaked off like a whiteboard marker.) 

Luckily I'd also labeled each tube to indicate the treatment, and these marks (other sharpies) didn't wash off.  The blue bars are the amount of crystal violet that stained tubes that had been pretreated with DNA.  The green bars are for tubes pretreated with just the buffer, and the pink bars are for tubes pretreated with buffer and then given 1 µg DNA/ml in solution in the cell culture.

If we set aside the murR749 hypercompetent mutant, I can make a few (weak) generalizations.  First, my DNA pretreatment didn't increase the amount of staining, and thus didn't increase the numbers of cells adhering to the sides of the tubes.  Second, adding dissolved DNA to the cultures may have slightly increased the amount of staining.  Third, the use of the sxy hypercompetent mutant or either non-competent mutant (sxy- or pilA-) didn't affect the amount of staining.

The murE749 mutant had higher staining than the other strains, especially if I ruthlessly assign the high 'unknown' to it.  This strain's staining was also higher in the first version of this experiment.

Is any of this worth following up on?  I don't think I'll bother to repeat this experiment using a more reliable Sharpie.  Should I put more effort into getting DNA attached to a surface?  I think first I should finish my post about what biofilms are...

No DNA-enhanced biofilms

Yesterday I tested whether pre-coating glass tubes with DNA helps competent cells form biofilms.  The answer is clearly No, but the results are nevertheless interesting, in a "That's peculiar!" way.

I did pretty much what I had planned (see previous post):  I added 2 ml of a DNA solution to new glass culture tubes (in high-salt, low-pH), left it for an hour at room temperature, removed the solution and let the tubes dry for several hours at 37 °C.  I then rinsed these tubes and untreated tubes with the high-salt low-pH buffer.  I then added 3 ml of either high-density (~2x10^8 cfu/ml) or low density (?~10^7 cfu/ml?) cultures of the five strains I wanted to test, and left them for either 4 hr (high density cultures) or 18 hr (low density cultures) at 37 °C, just sitting in a rack.  When the time was up I dumped out the cells, rinsed the tubes once with phosphate-buffered saline (no vortexing), and added 2 ml of a 0.1% solution of crystal violet in water.  (I tried putting the crystal violet in my high-salt low-pH buffer but it wouldn't dissolve).  I let the tubes sit for 10 min, dumped out the crystal violet, rinsed them with water, and let them dry.  Then I resuspended the dye in 1 ml of 95% ethanol and measured its absorbance.  The amount of dye that stuck to the tubes should measure the amount of cells that were stuck to the tubes.

I was hoping that the DNA treatemnt would increase the number of cells sticking to the sides of the tubes, especially for the two hypercompetent mutants (sxy-hyp and murE-hyp), but not for the non-competent mutants (sxy- and pilA-).

The graph shows that the DNA treated tubes (light blue and light green) had LESS, not more, stain.

This could have just meant than my pre-treatment didn't work - that the DNA had washed off the tubes before I added the cells.  But that wouldn't explain why the untreated tubes had more cells that didn't wash off, especially after the long incubation.  Instead, the DNA treatment appears to have done something that actively decreased cell adhesion.

My first look at the 18 hr cultures had me expecting a very different result.  In all of the cultures in the no-DNA tubes, most of the cells had sunk to the bottom of the tube, but most of the +DNA tubes were cloudy all the way up.  This led me to think that they had thick biofilms, but now I think that the cells were just more evenly suspended in the medium.  Unfortunately I didn't measure the cell densities or anything else, or do replicates, or even carefully check which of the +DNA tubes looked less cloudy than the others (I think it was the pilA mutant).

So I guess I should repeat the whole thing.  But first I should put some thought into possible explanations...  ...OK, I have no idea.  There shouldn't have been much DNA in solution in the +DNA tubes, given that I did rinse them before adding the cells.  But I could test this by having tubes where I just added 1 µg of DNA in solution to the culture.  Might the soaking in DNA have modified the physical properties of the glass surface in some way?  This time I should treat the -DNA control tubes exactly the same way I treat the +DNA tubes.  I guess I also need to do replicates this time.  I won't bother with the high-density 4-hr incubations, I'll just do overnight ones that start at low cell density.

I'll also count each culture's cfu/ml at the start of the incubations, and check the ODs at the end (with and without mixing up any settled cells.  And I'll be more meticulous in my washing steps.

Better go pour a few plates and start preparing the tubes...

DNA and biofilm formation, planning

I want to test whether their ability to bind DNA helps competent cells form or join biofilms. 

The standard way to test for biofilm formation is to incubate cells in a polystyrene microtiter-well plate, remove the unbound cells, and stain the remaining bacteria with crystal violet.  But I don't know anything about whether DNA sticks to polystyrene (I can only find bapers about chemical methods of attachment, so I don't think it spontaneously sticks), and I think it's better to do the test under conditions where biofilms don't form easily.

As a preliminary test, I first want to coat the inside of glass culture tubes with a film of DNA.  I'll then add dilute H. influenzae cells, either wildtype or constitutively competent, and incubate overnight (with or without constant mixing? probably I'll try both).  The on-line sources say that DNA binds 'avidly' to glass under conditions of high salt and low pH (below 7.5).

So I'll prepare a high-salt low-pH stock of H. influenzae chromosomal DNA (100 µg/ml DNA, 1 M NaCl, 50 mM Tris pH 7.0).  I have an old high-concentration DNA stock somewhere.  I'll add 2 ml of this to new (sterile)glass culture tubes and let them sit for 1 hr at 37 °C.  Then I'll pour out the DNA (saving it for next time), and leave the tubes to dry  at 37 °C overnight.  In the morning I'll fill the tubes with 1M NaCl 50 mM Tris pH 7.0, leave them for 30 min, vortex them and discard the wash solution.  Then I'll add 5 ml of cell culture in sBHI, at a density of ~ 10^7 cfu/ml, and incubate the tubes at 37 °C for 5 hr or overnight.  Then I'll remove the cells, and add crystal violet (0.05%) to stain the biofilm.  After 10 min I'll wash the tubes with water twice, and then dissolve the remaining crystal violet in 95% ethanol and measure its absorbance at 570 nm.

What cells will I use?  Wildtype cells, hypercompetent mutants (sxy-1, murE749), noncompetent mutants (sxy-, cya-, pilA-).  I'll have control tubes with no DNA, and tubes with added DNase I.

Submitted!

Back to the bench...

Well, not quite yet, but very soon.  The CIHR proposal is in excellent shape - we're doing a final read through and then final revisions (just polishing) on Monday, and then I'll click 'Submit' two days ahead of the deadline (a new record).

It's in such good shape that I'm already preparing to get back in the lab.  The first step is updating the Table of Contents of my lab notebook.  This is just a Word file that lists each experiment's number and date with a few words or sentences describing it.  Having it is very useful as I can search for any word to find the relevant experiments (which I might otherwise have forgotten about).  The process of updating it is also very useful, as I have to read through my notebook and summarize each experiment.  That's what I've been doing, for the work I've done since January.

This readthrough showed that I have two projects ongoing.  One is the optical tweezers work.  Now that the system is working reasonably well, it's time to make some well-characterized DNA-coated beads (measuring the amount of DNA on each bead) and start trying to get cells to grab onto the DNA.  It would be good to demonstrate this at the bench as well as trying to see it with the tweezers apparatus (abbreviated 'OT' by its creator).

The other project is the purine work on the regulation of competence.  We now have the mutants we need, properly verified by PCR, so it's time to do some more rigorous phenotyping.

Bead and cells

A figure for our CIHR grant proposal.

Phenotypes of retraction and anti-backsliding mutants

One component of the CIHR proposal we're working on is identifying mutants that are unable to retract their pseudopili ('retraction mutants') or to preventing DNA from sliding back out after it has been partly pulled in ('anti-backsliding mutants').  These mutants are expected to have similar but not identical phenotypes.  The retraction mutant should be able to bind DNA at the cell surface but not take up any of it into the periplasm, so when cells are incubated with 32P-labeled DNA, all of the 'cell-associated' DNA should be removed by DNase I.  The anti-backsliding mutant should also bind DNA, but it would be able to bring some DNA into the periplasm.  This uptake should be inefficient, especially if the next step (translocation into the cytoplasm) is blocked by another mutation or by using circular DNA.  So uptake should be reduced but probably not eliminated.

But the screens for these mutants aren't very good, so I need to think more about this.

Consider the retraction mutants first:  These mutants should be able to bind DNA, but that doesn't mean they will have the same level of cell-associated radioactivity as wildtype cells.  That depends on whether the uptake machinery is reused to take up more than one DNA fragment.  To explain this better, here's an extreme example:  Imagine that wildtype cells have only one DNA-binding structure on their surface.  After DNA binds to this structure, the DNA is passed to an uptake machine (again only one per cell) which pulls it across the outer membrane into the periplasm.  In species A, the structure is now free to bind another DNA fragment and pass it to the uptake machinery, and then another, and then another.  In species B, each structure (or each uptake machine) can be used only once.  When we compare the amounts of 32P-DNA associated with cells of species A and species B, species A will have four times as much.  Now consider a mutant of each species whose uptake machine is unable to pull DNA in at all.  These cells can still bind DNA but they can't take it up.  The species A mutant will only have 25% as much cell-associated DNA of wildtype species A cells, but the species B mutant will have 100%.

Is H. influenzae's DNA uptake like species A or species B?  We have suspected it's more like species B (i.e. uptake machinery isn't reusable), but the evidence for this is mainly just that the number of transformants doesn't keep increasing with increasing time or increasing DNA concentration, as if the uptake machinery had been used up.  But the same effect may not be seen with DNA uptake experiments (I have one example where it isn't), which would mean that the bottleneck is at a later step (DNA translocation or recombination).  I think we need to carefully investigate this first, so we'll know what phenotype to expect of our postulated retraction mutants.  The post-doc has some newer uptake data that may address this.

The other issue is how we measure cell-associated DNA.  The standard procedure is to incubate competent cells with a 'saturating' amount of DNA labeled with 32P (or 33P) and wash the cells by centrifuging them, resuspending them in fresh medium (with vigorous vortexing), centrifuging them again, resuspending them again, and probably centrifuging and resuspending them one more time.  The goal is to remove all the DNA that's in the medium but leave all the DNA that's stuck to or inside the cells.  This procedure should be fine for DNA that's inside the cells, but we don't really know how well this works for DNA that's just bound to the outside of the cells.  Does the vigorous vortexing pull loosely bound DNA off the cells?  The answer probably has something to do with Reynolds numbers, but that's beyond my expertise.  In Neisseria, does it break off the pili that the DNA may be bound to?  The RA probably can answer this, not because she knows about Reynolds numbers but because she's worked with Neisseria.

So I'm considering a different way of washing the cells.  We routinely use filtration to collect and wash cells when we're transferring them to competence medium, so why not also use it to collect and wash cells in DNA-binding assays?  We could first dilute the cells+DNA into a large volume of medium (100-1000-fold dilution, and then collect the cells by filtration (perhaps using only gentle suction to minimize shearing forces at the filter).  We can then easily wash the filter with lots more medium to make sure all the unbound DNA is removed.  Then we can just pop the filter into a scintillation vial for counting.  To detect only DNA that has been taken up, we can add DNase I to the cells, dilution mix or wash.   The dilution and washing medium should be cold or at room temperature to stop uptake of DNA that's already bound.  Clogging of the filter isn't a problem because we'd be using only ~1 ml of cells, and the medium is cheap so the dilution and washing volumes are limited only by the capacity of the collection flask under the filter.  The filters cost a couple of dollars each, but I think this would be well worth the cost.

We also can't be sure that the mutant's defect will be due to defective retraction of the postulated pseudopilus, but that should be a separate post.