It's time to revisit the arsenic-using bacteria paper. I wrote about it on the day it came out, mainly to try to correct a lot of the poorly done reporting in the general press. These bacteria weren't another form of life, they weren't from another planet, they weren't (as found) living on arsenic (and they weren't "eating" it), and so on.
Now it's time to dig into the technical details, because it looks like the arguing over this work is coming down to analytical chemistry. Not everyone is buying the conclusion that these bacteria have incorporated arsenate into their biomolecules, with the most focused objections being found here, from Rosie Redfield at UBC.
So, what's the problem? Let's look at the actual claims of the paper and see how strong the evidence is for each of them:
Claim 1: the bacteria (GFAJ-1) grow on an arsenate-containing medium with no added phosphate. The authors say that after several transfers into higher-arsentic media, they're maintaining the bacteria in the presence of 40 mM arsenate, 10 mM glucose, and no added phosphate. But that last phrase is not quite correct, since they also say that there's about 3 micromolar phosphate present from impurities in the other salts.
So is that enough? Well, the main evidence is that (as shown in their figure 1), that if you move the bacteria to a medium that doesn't have the added arsenate (but still has the background level of phosphate) that they don't grow. With added arsenate they do, but slowly. And with added phosphate, as mentioned before, they grow more robustly. It looks to me as if the biggest variable here might be the amount of phosphate that could be contaminating the arsenate source that they use. But their table S1 shows that the low level of phosphate in the media is the same both ways, whether they've added arsenate or not. Unless something's gone wrong with that measurement, that's not the answer.
One way or another, the fact that these bacteria seem to use arsenate to grow seems hard to escape. And they're not the kind of weirdo chemotroph to be able to run off arsenate/arsenite redox chemistry (if indeed there are any bacteria that use that system at all). (The paper does get one look at arsenic oxidation states in the near-edge X-ray data, and they don't see anything that corresponds to the plus-3 species). That would appear to leave the idea that they're using arsenate per se as an ingredient in their biochemistry - otherwise, why would they start to grow in its presence? (The Redfield link above takes up this question, wondering if the bacteria are scavenging phosphorus from dead neighbor cells, and points out that the cells may actually still be growing slowly without either added arsenic or phosphate).
Claim 2: the bacteria take up arsenate from the growth medium. To check this, the authors measured intracellular arsenic by ICP mass spec. This was done several ways, and I'll look at the total dry weight values first.
Those arsenic levels were rather variable, but always run high. Looking at the supplementary data, there are some large differences between two batches of bacteria, one from June and one from July. And there's also some variability in the assay itself: the June cells show between 0.114 and 0.624% arsenic (as the assay is repeated), while the July cells show much lower (and tighter) values, between 0.009% and 0.011%. Meanwhile, the corresponding amount of phosphorus is 0.023% to 0.036% in June (As/P of 5 up to 27), and 0.011 to 0.014 in July (As/P of 0.76 to 0.97).
The paper averages these two batches of cells, but it certainly looks like the June bunch were much more robust in their uptake of arsenate. You might look at the July set and think, man, those didn't work out at all, since they actually have more phosphorus than arsenic in them. But the background state should be way lower than that. When you look at the corresponding no-arsenic cell batches, the differences are dramatic in both June and July. The June batch showed at least ten times as much phosphorus in them, and a thousand times less arsenic, and the July run of no-arsenate cells showed (compared to the July arsenic bunch) 60 times as much phosphorus and 1/10th the arsenic. The As/P ratio for both sets hovers around 0.001 to 0.002.
I'll still bet the authors were very disappointed that the July batch didn't come back as dramatic as the June ones. (And I have to give them some credit for including both batches in the paper, and not trying just to make it through with the June-bugs). One big question is what happens when you run the forced-arsenate-growth experiment more times: are the June cells typical, or some sort of weird anomaly? And do they still have both groups growing even now?
One of the points the authors make is that the arsenate-grown cells don't have enough phosphorus to survive. Rosie Redfield doesn't buy this one, and I'll defer to her expertise as a microbiologist. I'd like to hear some more views on this, because it's a potentially important. There are several possibilities - from most exciting to least:
1. The bacteria prefer phosphorus, but are able to take up and incorporate substantial amounts of arsenate, to the point that they can live even below the level of phosphorus needed to normally keep them alive. They probably still need a certain core amount of phosphate, though. This is the position of the paper's authors.
2. The bacteria prefer phosphorus, but are able to take up and incorporate substantial amounts of arsenate. But they still have an amount of phosphate present that would keep them going, so the arsenate must be in "non-critical" biochemical spots - basically, the ones that can stand having it. (This sounds believable, but we still have to explain the growth in the presence of arsenate).
3. The bacteria prefer phosphorus, but are able to take up and incorporate substantial amounts of arsenate. This arsenate, though, is sequestered somehow and is not substituting for phosphate in the organisms' biochemistry. (In this case, you'd wonder why the bacteria are taking up arsenate at all, if they're just having to ditch it. Perhaps they can't pump it out efficiently enough?) And again, we'd have to explain the growth in the presence of arsenate - for a situation like this, you'd think that it would hurt, rather than help, by imposing an extra metabolic burden. I'm assuming here, for the sake of argument, that the whole grows-in-the-presence-of-arsenate story is correct.
Claim 3: the bacteria incorporate arsenate into their DNA as a replacement for phosphate. This is an attempt to distinguish between the possibilities just listed. I think that authors chose the bacterial DNA because DNA has plenty of phosphate, is present in large quantities and can be isolated by known procedures (as opposed to lots of squirrely little phosphorylated small molecules), and would be a dramatic example of arsenate incorporation. These experiments were done by giving the bacteria radiolabeled arsenate, and looking for its distribution.
Rosie Redfield has a number of criticisms of the way the authors isolated the DNA in these experiments, and again, since I'm not a microbiologist, I'll stand back and let that argument take place without getting involved. It's worth noting, though, that most (80%) of the label was in the phenol fraction of the initial extraction, which should have proteins and smaller-molecular-weight stuff in it. Very little showed up in the chloroform fraction (where the lipids would be), and most of the rest (11%) was in the final aqueous layer, where the nucleic acids should accumulate. Of course, if (water-soluble) arsenate was just hanging around, and not being incorporated into biomolecules, the distribution of the label might be pretty similar.
I think a very interesting experiment would be to take non-arsenate-grown GFAJ-1 bacteria, make pellets out of them as was done in this procedure, and then add straight radioactive arsenate to that mixture, in roughly the amounts seen in the arsenate-grown bacteria. How does the label distribute then, as the extractions go on?
Here we come to one of my biggest problems with the paper, after a close reading. When you look at the Supplementary Material, Table S1, you see that the phenol extract (where most of the label was), hardly shows any difference in total arsenic amounts, no matter if the cells were grown high arsenate/no phosphorus or high phosphorus/no arsenate. The first group is just barely higher than the second, and probably within error bars, anyway.
That makes me wonder what's going on - if these cells are taking up arsenate (and especially if they grow on it), why don't we see more of it in the phenol fraction, compared to bacteria that aren't exposed to it at all? Recall that when arsenic was measured by dry weight, there was a real difference. Somewhere there has to be a fraction that shows a shift, and if it's not in the place where 80% of the radiolabel goes, then were could that be?
I think that the authors would like to say "It's in the DNA", but I don't see that data as supporting enough of a change in the arsenic levels. In fact, although they do show some arsenate in purified DNA, the initial DNA/RNA extract from the two groups (high As/no P and no As/high P) shows more arsenic in the bacteria that weren't getting arsenic at all. (These are the top two lines in Table S1 continued, top of page 11 in the Supplementary Information). The arsenate-in-the-DNA conclusion of this paper is, to my mind, absolutely the weakest part of the whole thing.
Conclusion: All in all, I'm very interested in these experiments, but I'm now only partly convinced. So what do the authors need to shore things up? As a chemist, I'm going to ask for more chemical evidence. I'd like to see some mass spec work done on cellular extracts, comparing the high-arsenic and no-arsenic groups. Can we see evidence of arsenate-for-phosphate in the molecular weights? If DNA was good enough to purify with arsenate still on it, how about the proteome? There are a number of ways to look that over by mass-spec techniques, and this really needs to be done.
Can any of the putative arsenate-containing species can be purified by LC? LC/mass spec data would be very strong evidence indeed. I'd recommend that the authors look into this as soon as possible, since this could address biomolecules of all sizes. I would assume that X-ray crystallography data on any of these would be a long shot, but if the LC purification works, it might be possible to get enough to try. It would certainly shut everyone up!
Update: this seems like the backlash day. Nature News has a piece up, which partially quotes from this article Carl Zimmer over at Slate.