You'll all remember the big news about the arsenic-using bacteria - that Science paper from last December. What you may not realize is that the paper is only now coming out in print. The delay seems to have been to allow time for an extraordinary number of responses to be published at the same time. I'll summarize those, and the counterarguments made by the original authors.
Rosie Redfield of UBC, whose blog was one of the earliest criticisms of the paper, objects that the culture media used were not pure. She maintains that there was enough phosphate in the growth medium to account for all the cell growth seen, without having to invoke arsenic-containing DNA. She also has a problem with the way that the DNA fractions in the original paper were (not) purified, pointing out that the procedures used could easily drag along many contaminants.
In response, Wolfe-Simon et al. don't find the trace-phosphorus objection compelling, they say, because the arsenic-stimulated organisms were grown under the same P background as the controls at that point, and the arsenic group grew much better. As for the DNA purification, they go over their procedures, state that they didn't see evidence of particulate contamination, and point out that negatively-charged arsenate is unlikely to stick to DNA unless it's covalently bound.
A team from CNRS and JPL makes the point (as others did at the time of first publication) that arsenic's own redox chemistry makes the original assertion hard to believe. Under all known physiological conditions, arsenate should be less stable than arsenite, and arsenite can't be a plausible substitute for phosphate (even if you buy that arsenate can). They also believe that the bacteria are running on residual phosphorus: "GFAJ-1 appears to do all it can to harvest P atoms from the medium while drowning in As. . ."
Wolfe-Simon et al. reply by saying that they specifically looked for reduced arsenic species in the cells, without success, and suggest that something must be stabilizing arsenate that no one has yet seen or considered.
Another team response, from Hungary and Johns Hopkins, objects to the way that the P:As ratios were calculated in the paper. The error for the dry-weight arsenic percentage in the bacteria is larger than the value itself, so you can't really be sure that there was no arsenic at all. The mass spec data used in the paper, they say, also have such high fluctuations as to make the numbers unable to support the paper's claims.
In response, Wolfe-Simon et al. say that they don't find the arsenic numbers to be all that variable, considering the conditions. And the phosphorus numbers don't vary much at all, by comparison, and the arsenic numbers are always higher.
Stefan Oehler, from Greece, asks why density gradient centrifugation of the supposed arsenic-containing DNA wasn't done (as did other observers when the paper came out). As-DNA should be heavier. Comparing hydrolysis rates of the As-DNA with the normal phosphate form "could also have been easily done", and he says that without these data, the paper is unconvincing. One major suggestion he has is to see how and where the bacteria incorporate radioactive arsenic.
David Borhani (ex-Abbott) has objections that are similar to some of the others. He's not convinced that the "-P" media really don't have enough phosphorus left in them to explain the results, and says that the agarose gels shown are hard to square with the paper's claims. (The phosphorus-containing DNA looks more degraded than the putative arsenic-containing sample, for example, and the DNA being compared is of different sizes to start with). He has the same problems with the error bars as mentioned above.
Steven Benner (who, interestingly, appeared at the original press conference back in December, albeit not as a cheerleader), comes at the problem from a chemical angle. The rate constants for arsenate hydrolysis gives you an expected half-life for such esters inside a cell of seconds to minutes (at best), which doesn't seem feasible for use in biomolecules. He goes over several possibilities for ways to make such linkages more stable - or for judging the literature on arsenate stability to be wrong - and can't make any of them work. Another big problem is that the phosphates in DNA have to survive as such for numerous steps in the cell, and it's hard to see how arsenate could substitute across such a wide range of biochemistry. He'd also like to see the As-DNA subjected to hydrolysis and to enzymes such as DNA kinase or exonuclease, to see how it behaves. "Above all", he says, do the radioactive arsenic experiment.
In response, Wolfe-Simon et al. say that there's very little data on the stability of arsenate esters of anything but very small molecules - steric hindrance, among other things, would be expected to make the bioesters more stable. They refer to a paper showing that arsenate esters of glucose were much more stable than expected, for example.
Patricia Foster of Indiana suggests that the process of raising the GFAJ-1 bacteria selected for mutants that have lost their phosphate inorganic transporter (Pit) system, but have pumped up their phosphate-specific transport (Pst) system. It's been shown in E. coli, she points out, that arsenate poisons the former transporter, but actually stimulates the latter, which would account for the apparent stimulatory effect of arsenic on GFAJ-1.
Wolfe-Simon et al. respond by saying that if the Pst pathway were stimulated, they'd expect to see evidence of arsenate detoxification pathways (thioarsenate, methylation, reduction), and they don't. (That seems weird to me - surely the organism, no matter what, is seeing a lot more arsenate than it can use, and would have to do some of these things?)
Finally, James Cotner and Edward Hall of Minnesota and Vienna, respectively, note that their own work was cited in the original paper on the phosphorus content of bacteria. They object, though, saying that their phosphorus-rich experiment make a poor comparison with the GFAJ-1 case. In fact, they say, they've now published a survey of the elemental content of freshwater bacteria, and that these can actually be highly depleted in phosphorus. The phosphorus content measured in GFAJ-1 does not, in fact, fall outside of the range seen in organisms grown under naturally P-limiting conditions.
Wolfe-Simon et al. reply that Cotner and Hall's numbers are taken from individual bacteria at the low end of the range, not whole populations, making them a poor comparison. Their whole-population values, they say, are actually similar to their own phosphorus control cultures, and are both higher than the arsenate-grown bacteria.
So, in the end, the authors are sticking to their original arsenic hypothesis. They agree that analyzing DNA after separating it from the gels would be a useful experiment (as Redfield and other propose), and they also say that they did not mean to suggest that the GFAJ-1 bacteria have a "wholesale" subsitution of arsenate for phosphate, just that they do have some. And they're making GFAJ-1 available to people who want to take a crack at their own experiments.
This is really a remarkable exchange, but mostly due to its sheer concentration in time and in publication. But this is exactly how science is done, although it usually happens a bit more slowly and in a more disorganized fashion than what we're seeing here. But these extraordinary claims have brought an extraordinary response.
I think that things have gone as far as they can with the data from the original paper, and it's fair to say that that's not far enough to convince a lot of people. Next step: more data, and more experiments. One way or another, this will get detangled.