Dr. Andy

Reflections on medicine and biology among other things

Tuesday, March 29, 2005


Reader Scott Kern, who knows a lot more than me about this area and has given it a lot of thought, sends this critique of the HOTHEAD reversion, crazy RNA memory paper in nature, I blogged about previously:
As a cancer geneticist who spends a lot of time trying to expunge mutation artifacts from our genetic studies, I'm appalled at the sloppy presentation of the arabidopsis reversions in Nature. No supplemental data, a methods section shorter than the Abstract, near absence of methodologic details in the text, etc.

In the first paragraph of the second page, did they really use allele-specific PCR to "clearly" show a conclusion? In other words, they purchased the chosen sequence by mail, then found the same sequence when the mail-order oligos were used in an artifact-prone method? All withoutshowing any controls for the specificity of the allele-specific method or for how the results might be potentially affected by small sample size (which by reducing the number of DNA templates, increases the influence of PCR-introduced errors).

In figure 1a, what was the restriction site used? Did it occur naturally in the sequence (I don't see it in the figure showing the sequences), or was it artifactually introduced during PCR? Why does the top allele in Figure 1A appear so much brighter than the restriction-cut allele just below it -are the alleles not in molar equivalence? If this is a two-allele system,molar equivalence would seem to be required.

In the Southern blot, what was the probe?

What were the primer sequences used for the assays ?

If the altered sequences were found by one method, could they be confirmed by finding them with use of another method having non-overlapping artifactual tendencies? I note that they didn't use phage lifts or allele-specific ligation to quantitate the allelic ratio of the revertant alleles, as had been done 15 years earlier to provide the necessary controls for the study that showed infrequent mutant genes in stool samples of colorectal cancer patients.

Why no negative controls - such as non-embryoid parts of the hth/hth and> HTH/HTH plants whose DNA had been isolated in minute amounts similar to the technique used for the seeds?

Why no primary data from gene sequencing in any of the figures? Did Nature refuse to publish the primary data even in supplemental form?

Do we really think that 38% of samples had gene reversion (table 2)? That would be a higher rate of gene conversion in trans than any other recombination system, including yeast.

Why no coded samples? When the infrequent gene mutations in pancreatic ductal lesions and in stool samples of pancreatic cancer patients werefound 10 years ago, the samples were tested blindly. Wouldn't everyone would do this or some similar form of investigator blinding? And why not do the studies in a lab that had never previously seen studies of the HTH gene? This has been done when other authors wanted to quantitate gene mutation prevalence rates in cancer patients.

I suppose Nature will once again call in the Amazing Randi to investigate the authors, just like they did with their water memory paper in 1988.

I don't claim to know whether the data in this paper are valid, but certainly the methods are not presented in adequate detail nor in adequate confirmatory depth to judge. Until then, discussing this paper is a waste of time.

I'll agree with Scott and say as I did last time that before you publish a paper in Nature that calls into question much of how we think about genetics, you need to have more than suggestive data; you need to have things nailed down airtight with all the data and controls everyone would want.


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