Existence of RNA Genome or Fertility Selection?

A new paper by Susan Lolle, Robbert Pruitt, and collegues at Purdue Univeristy is making some press. The NY Times covered it in a story entitled, Startling Scientists, Plant Fixes Its Flawed Gene. Carl Zimmer has discussed it on his blog: Move Over, Mendel (But Don’t Move Too Far). The paper is entitled, “Genome-wide non-mendelian inheritance of extra-genomic information in Arabidopsis.” It was quickly published in Nature this week, and is now available as an advanced access publication. I think Nature in its rush to publish cutting edge science has (once again) published a paper of fantastic claims that could use a little more support. I will explain below.

In a 1998 paper, the two main author identified and studied the genes that are involved in organ fusion in Arabidopsis thaliana. They subsequently noticed that one of their genes, hothead (HTH/hth) showed an extremely high rate of reversion from null (hth) to wild-type (HTH). The rate of reversion for several different null alleles, 0.040 - 0.082, was very much higher than expected from typical mutation rates.

They initially suspected that their stocks had been contaminated with wild-type seeds or that their plants were out-crossing with wild-type pollen. However, they genotyped embryos and demonstrated the existence of revertant embryos, which ruled out seed contamination. They next ruled out pollen contamination by demonstrating that pollen from an hth/hth plant can transmit the HTH allele.

Sequencing ruled out the involvement of transposons and repeated sequences. They also tested whether the gene had a higher mutation rate but ruled it out due to lack of silent nucleotide substitutions. They ruled out gene conversion through non homologous recombination because they found no suitable donor sequence in the genome. They also found that molecular markers were genetically unstable (i.e. high mutation rate) in hth/hth plants but not in HTH/HTH plants. This argued for a genome wide effect.

With all these options investigated and ruled out, the authors proposed that genetic information was transmitted not only in the genome but in an additional way. This secondary information was then restoring the HTH allele in some hth/hth individuals. The researchers proposed (double-stranded) RNA as the possible vehicle for this secondary storage.

I think that Lolle et al. missed one important mechanism when they were considering possible explanations: selection. Before I continue, I want to point out what else I think is missing in the study: direct sequencing of male gametophytes to determine their haplotypes, some statistical tests, hth alleles not due to point mutations, knowledge of the rate of silent mutation rates for wild-type hothead genes, and probably a few other things.

I prefer selection over the explanation proposed by the authors, since it is a well established mechanism for changing allele frequencies and it can explain why the reversions only occur in pollen. The selection I’m proposing is the result of pollen competition; i.e. HTH pollen fertilizes ovules better than hth pollen. With pollen having a much larger population size than ovules, there is a greater chance at producing a revertant through mutation, at which point selection can act upon it. HTH could also be important for ovule success, but the lower population size of ovules and less chances for competition would make the effect less likely to show up.

What about the fact that genetic instability was found in other markers in hth/hth individuals? Well, I suspect that the loss of a functioning hothead gene increases the global mutation rate, which affects those markers too. Perhaps this is the reason why HTH pollen is selected for; it puts the mutation rate back in order.

Why didn’t the researchers find silent mutations in revertant HTH? Well, if the revertant HTH is selected because it fixes mutation rates, then individuals that revert sooner than later may be preferred. The fastest way to produce revertant HTH is to reverse the point mutation that produced hth. The researchers might not have had the power to detect silent mutations in revertant HTH because they only sequenced three lines.

What about the fact that HTH/hth heterozygotes produce hth/hth individuals at nearly 25%? Doesn’t that exclude pollen selection? Well, the advantage of HTH pollen over hth pollen may be a paternally influenced trait that only shows up from hth/hth pollen donors. The advantage may also be frequency dependent and only occur when HTH is rare.

The paper by Lolle et al. involves a really interesting system, but I seriously doubt that their proposed explanation will hold up. I think selection, which isn’t discounted by their results, is a better explanation. It is really going to be interesting as more papers and other labs try to figure out what is going on in this system.

References

  • Lolle SJ et al. (2005) Nature 434: 505-509.
  • Lolle SJ et al. (1998) Genetics 149: 607-619.
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Posted by Craig Kaplan on March 24, 2005 1:22 AM

I think the paper discusses “reversion” frequency. In no place do the authors’ identify increased mutation freqency at any particular site. Additionally, I’m not sure the model proposed here can explain that the paper describes much higher reversion frequency for non-hth mutations in the hth background (they looked an allele of another gene, as well as silent SNPs). I think this rules out selection for HTH over hth.

Posted by Reed A. Cartwright on March 24, 2005 2:32 AM

The authors’ discussion of mutation is incomplete. They only tested whether HTH revertants were caused by a higher mutation rate. They discounted this due to a lack of mutations in the hth revertants. But there are some problems with this analysis.

1) They based their expectations on the high frequency of revertants being based solely on a high mutation rate. This would not discount an increased mutation rate and selection working together.

2) They only sequenced three HTH revertants. This gives them a low power to test for high mutation rates in hth if hth itself is the cause of the high mutation rates.

3) There was no HTH/HTH control for silent mutations. They don’t tell us what the wild-type rate of sequence mutation is for this gene.

4) They did not analyze the sequences of the unstable non-hth markers for silent mutations. Thus they did not discount that instability in their non-hth markers was due to higher mutation rates.

Posted by Nick Matzke on March 24, 2005 10:42 AM

Wouldn’t be the first time that selection turned out to be behind an apparent violation of the normal rules of heredity.

How many pollen grains does an Arabidopsis flower produce? Say, that only 100 out of every 10^6 hth pollen grains from an hth/hth flower produced viable pollen. Further, let’s say that 1 out of every 10^6 hth grains 1 was a revertant to HTH. This would make it appear like HTH revertants appeared with a frequency of 1/100.

If hth pollen from HTH/hth flowers was basically normal, this would explain the 25% rate of production of hth/hth from HTH/hth - HTH/hth crosses.

Posted by Timothy McDougald on March 24, 2005 11:02 AM

Would the fact that Arabidopsis engages in selfing have any impact?

Posted by Craig Kaplan on March 24, 2005 5:47 PM

They only observed reversion, even at supposedly phenotypically silent SNPp. They never observed a de novo mutation, or did not state that they did. I think this is a very strong argument against selection. Spotaneous mutation coupled with incredibly strong selection is certainly normally high enough to revert a single base in the genome, but to revert basically other alleles outside of hth, as well as other SNPs (and only revert to one background or another, not generate new mutations) really argues that this is not selection and mutation acting together. I just don’t think you can get around it.

Posted by Reed A. Cartwright on March 24, 2005 8:52 PM

Craig,

As far as I can tell from the paper, the authors didn’t analyze the sequence of the non-hth markers. They are not very clear in the paper on how these markers work, and I have never dealt with them nor had the time recently to research them. I suspect that these markers are not detected through sequencing but through blotting, giving a polymorphism of presence versus absense. Such analysis will be ill suited to detect whether the markers reverted their sequences to the exact sequence of Col or Ler.

Posted by Ivan on March 24, 2005 11:49 PM

They did detect HTH/HTH embryos from hth/hth plants even though they were rare. The selection argument doesn’t really work for ovules because there isn’t much competition between them for pollen.

Average pollen grains/flower = 156
Science, Vol 274, Issue 5292, 1535-1537 , 29 November 1996
That gets you ~50 seeds/fruit.

The markers are all CAPS markers: you PCR up a band and then cut with a restriction enzyme to get a different banding pattern. So you are basically looking at either (1) the frequency of mutation of the 6 base restriction site, or (2) reversion to the grandparent allele. If it’s (1) you are looking at a screamingly high mutation rate and you would expect to see more point mutations in the hth gene when they went back to sequence the revertants.

They actually sequenced 9 plants, 3 each for 3 separate lines.
“To test this we determined the complete DNA sequence of the
coding region of the HTH gene after three independent reversion
events in each of three independently derived mutant hth alleles
(hth-4, hth-8 and hth-10).”

I don’t really buy the “pollen competition in the hth/hth background would be invisible in the hth/HTH background” argument. I think you would see an effect like you see with this pollen mutant….
http://www.pnas.org/cgi/content/full/101/25/9502…

and you should be able to see something in the +/- lines.

So, in summary, I don’t think your hypothesis is more likely than theirs. But your suggested experiments are all good except that it would be mega hard to sequence the individual male gametophytes. But more sequencing of other loci would be good. Additionally, I have to say that Nature & Science really make it hard to evaluate papers because of the size limitations of their articles. They should have sent this to PLOS Biology. It really is the way of the future.

I have to say it’s weird to be posting about science on a blog. I have taken a lot longer to write this than my usual blog comments, but a LOT shorter than anything I would write for a science publication. It makes me a little nervous, so if I have made a big boo-boo somewhere in the above, please forgive me. I would take more time, but I really should be working on that conference abstract. :)

Ivan

Posted by Reed A. Cartwright on March 25, 2005 12:20 AM

Ivan wrote:

They did detect HTH/HTH embryos from hth/hth plants even though they were rare. The selection argument doesn’t really work for ovules because there isn’t much competition between them for pollen.

It is true that selection couldn’t explain HTH/HTH embryos. I wish I knew what the rate was, but I don’t remember them saying it except to point out that it was rare. Actually, HTH/HTH embryos from hth/hth crosses would be a very good piece of data since it would be useful in dissecting the effects of mutation from the effects of pollen selection.

If it’s (1) you are looking at a screamingly high mutation rate and you would expect to see more point mutations in the hth gene when they went back to sequence the revertants.

Not really. That expectation assumes that hth is not the cause of the high mutation rate. Once hth reverts to wild-type, the mutation rate settles down to the wild-type rate, and the gene non longer experiences high mutation rates. If revertants are selected for, then the fewer mutations that hit that gene the better. This is where the experimental design of the paper suffers. They didn’t control for effects of selection. What they should have done is also sequence non revertants to see how they are accumulating silent mutations.

I don’t really buy the “pollen competition in the hth/hth background would be invisible in the hth/HTH background” argument.

What don’t you like about “paternal effect” or frequency dependent selection? I would really like to see some studies in which they varied the pollen proportion of HTH in the pollen population. That could help establish if it is a frequency dependent effect.

I think you would see an effect like you see with this pollen mutant ….

Can you be a little more specific?

So, in summary, I don’t think your hypothesis is more likely than theirs.

I think my main point is that the authors need to have considered more complex (i.e. realistic) evolutionary genetic situations before they proposed an alternative method of molecular heredity. I think the most important data that is missing is the actual biochemical function of the hothead gene. Knowing that would really help to figure out what is occurring in the double nulls.

Posted by Craig Kaplan on March 25, 2005 1:54 AM

I do agree with the latest comment. I think that the paper is provocative enough that I am glad they published it, though. I feel that this kind of paper is interesting enough that by being published it can convince people to look into results that don’t necessarily make sense. The papers that are published by bigshots that are completely crap (I’m thinking about a particular journal family- one can guess) are the ones that bug me the most. This paper might end up being new biology or a really interesting artifact, either way I will be keeping tuned.

Posted by PacRim Jim on March 25, 2005 12:06 PM

“Existence” not “Existance.”

Posted by Ivan on March 25, 2005 12:49 PM

“Actually, HTH/HTH embryos from hth/hth crosses would be a very good piece of data since it would be useful in dissecting the effects of mutation from the effects of pollen selection.”

Table2 from the paper:
in the hth-4 mutant 24% of the embryos were revertent +/-, 1% (2/233) were revertant -/-.
in hth-8 they say 38% of the 108 genotyped as +/- and 0 -/-.

In hth-10 %16 of 265 were +/- and 0 -/-.

Not really. That expectation assumes that hth is not the cause of the high mutation rate. Once hth reverts to wild-type, the mutation rate settles down to the wild-type rate, and the gene non longer experiences high mutation rates. If revertants are selected for, then the fewer mutations that hit that gene the better. This is where the experimental design of the paper suffers. They didn’t control for effects of selection. What they should have done is also sequence non revertants to see how they are accumulating silent mutations.

I don’t think I am making that assumption. I am assuming that the rate at which mutations occur is relatively stable across the genome. So that when you have a high mutation rate (whatever the cause) as they observe at the CAPS marker loci, you should be accumulating mutations at that rate in hth, and should therefore see other mutations along with the revertant.

Can you be a little more specific?

If you are seeing a selection effect that gets you 10% revertants in the contect of a flower producing ~150 pollen grains mating with ~50 ovules, i.e. a really strong effect. I think that you should see significantly less than 25% -/- from the het parent. They don’t say it, but I am assuming that they saw revertants and non revertants in the same silique (fruit) when they did the embryo genotyping. So your selection would be in the pollen competition step.

echoing the post by Craig, I think that this is a provacative paper even if their model is wrong. The observation of the revertant phenotype (whether by their method or another) wouldn’t make it in to Nature, but I would be relatively high profile. But I still do think they have something here and am looking forward to more papers on it.

Posted by Reed A. Cartwright on March 25, 2005 1:13 PM

Ivan wrote:

I don’t think I am making that assumption. I am assuming that the rate at which mutations occur is relatively stable across the genome. So that when you have a high mutation rate (whatever the cause) as they observe at the CAPS marker loci, you should be accumulating mutations at that rate in hth, and should therefore see other mutations along with the revertant.

Your “therefore” requires that assumption because it assumes that HTH and the mutation rate is not under selection. What I propose is that the revertant lines recovered were the lucky ones that fixed HTH while not accumulating other mutations that broke HTH or essential genes. The longer the mutation rate stayed high, the more likely it was that a deliterious mutation was going to occur. The successful revertants were the ones that happened earlier rather than latter in the mutation procoess.

Some of these issues could be settled if the authors used better controls, such as sequencing non revertant hth plants, or using an HTH allele that had silent mutations that could distinguish it from the hth alleles. As it is, their sequencing data cannot determine if revertant HTH was produced by a mutation from the hth allele or as a copy of an HTH allele in a previous generation.

I think that you should see significantly less than 25% -/- from the het parent.

That is true if we are dealing with classical directional selection of an standard genetic trait. However, that wouldn’t be true if the phenotype was the result of paternal effect or if it is the result of frequency dependent selection.

Posted by Craig Kaplan on March 25, 2005 11:13 PM

I just can’t see selection being so high for reversion of hth and against the proposed increase in accompanying increase in mutation rate when hth plants are fertile and hth progeny do not appear phenotypically unstable for other traits as you would expect after multiple generations of supposed mutagenesis. Given this mutagenesis you should really expect to see additional traits arising or silent mutations. I think this continues to argue strongly for some unknown or novel mechanism as proposed by the authors. We should know soon, however, I am sure this is being actively pursued. Apparently it has been around for awhile, and given the onslaught of attention, we should be hearing about this a lot. If only someone at Purdue had a blog to keep us closer to the action!

Posted by Jim Hu on March 26, 2005 1:12 AM

As someone pointed out over at the Loom, selection might work as an alternative hypothesis for the conversions at HTH itself, but it doesn’t account for the hth/hth-dependent conversions of the ecotype SNPs. The key point mentioned in the paper is that these conversions go in both directions, so to invoke selection you’d have to invoke heterozygote advantage for SNP alleles at several loci.

Posted by Reed A. Cartwright on March 26, 2005 11:15 PM

Jim Hu wrote:

As someone pointed out over at the Loom

That was me, after a brief read of the paper.

selection might work as an alternative hypothesis for the conversions at HTH itself, but it doesn’t account for the hth/hth-dependent conversions of the ecotype SNPs. The key point mentioned in the paper is that these conversions go in both directions, so to invoke selection you’d have to invoke heterozygote advantage for SNP alleles at several loci.

Selection probably doesn’t account for the changes in ecotype SNPs, but I think an increase in mutation rate would account for them.

Posted by Reed A. Cartwright on March 26, 2005 11:28 PM

Craig Kaplan wrote:

I just can’t see selection being so high for reversion of hth and against the proposed increase in accompanying increase in mutation rate when hth plants are fertile and hth progeny do not appear phenotypically unstable for other traits as you would expect after multiple generations of supposed mutagenesis.

I’m not proposing that it is selection for HTH individuals, but rather selection for HTH pollen over hth pollen. Mitotic drive is also a phenomenon that can cause deviations from Mendel’s law.

Given this mutagenesis you should really expect to see additional traits arising or silent mutations.

Correct, but the paper doesn’t discuss additional traits one way or another, and the experiments are not suitable to rule out silent mutations. The experiments presented in the paper are incomplete and lack suitable controls in many instances.

I think the most important data in explaining these results will be determining exactly at what part of the life cycle does high rate of revertant HTH genes arise. (I don’t think it is a flaw of the paper that the authors haven’t found this yet.) If it occurs in the embryos, then pollen competition is a possible force. If it occurs in the pollen, then mitotic drive is a possible force. Etc.

As I mentioned in another post, hothead appears to be homologous to mandelonitrile lyase. It will be interesting if similar phenotypes arise in other species where mandelonitrile lyase is knocked out.

Posted by Ivan on March 27, 2005 2:27 AM

I am at Purdue. Everyone here is talking about it as well. All I have heard is rumors at this point.

Posted by Scott Kern, Johns Hopkins on March 29, 2005 2:04 PM

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 without showing
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 (would exclude both small-sample amplification artifacts and chimerism)?

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 were found 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.

Posted by Jim Watson on March 30, 2005 1:03 AM

don’t see how it can be selection or an increased mutation rate if its genomewide reversion observed in the F2 generation to polymorphisms only present in one or other F0 grandparents.

However selection after the action of any non-mendelian restorative mechanism may explain the high percentage of revertants (as high as 38% criticised by Scott Kern, whose general point of lack of transparency i agree is a general problem with Nature and co). Revertant gametes may be healthier with one correct copy of Hothead rather than the mechanism itself being quite so ‘hot’ at its job. This is supported by the much lower reversion rate (2%) observed for other markers in the absence of hothead (table 3) which probably don’t give a any selctive advantage to gametes. Also the double revertants at I can expand on this if it isn’t clear…

More generally as far as criticising the paper… well they have really stuck out there necks if they haven’t thought of all the right internal checks and controls. And its 7 years since there initial observation so they haven’t rushed it out. I am sure they are well aware that they are staking there reputations.

Posted by Jim Hu on April 1, 2005 3:05 AM

Reed,

Looking back at the Loom, I thought I was agreeing with Craig Kaplan. I just posted a reply to Prof. Kern at the Loom, where he posted the same critique. I don’t think mutagenesis explains the ecotype SNP conversions…the probability of regenerating the same DNA changes would be too low, especially at so many loci.

Posted by Petr Gariaev on April 10, 2005 4:08 AM

We have obtained similar results on Arabidopsis with Muller’s mutation in 2003

http://www.self-managing.net/genetica/Zip/SFR.zi…

Results was published: П.П.Даряев, Е.А.Леонова, 2003, Странный мир волновой генетики. Журнал «Сознание и физическая реальность», т.8, №6, с.27-40.

Peter Gariaev, PhD. Moscow, Inst. Quantum Genetics. http://www.self-managing.net/genetica/

http://www.self-managing.net/genetica/zip.htm

Posted by lth on April 19, 2005 2:53 AM

Any new development on this? No more comments since Apr 1?

Posted by Reed A. Cartwright on April 19, 2005 1:52 PM

I haven’t been watching the literature. (I’m very bad about that.) I have gone back to read some earlier studies on the gene and it does seem likely to me that it serves to break down a chemical that is in a class of chemicals that are mutagens.

Posted by Dana R-S on April 28, 2005 4:53 PM

Dr Cartwright

I’m still trying to figure out the Lolle et al paper myself, but I see one flaw in your argument for selection:

Where are you getting the wild type allele that is being selected for?

I have no problem with selection being used to explain an increase in the frequency of the allele at the level of pollen health, but you seem to have forgotten to explain where the selected allele came from.

Is your problem with the reversion event itself, or their explanation?

Granted, they are missing some very important controls, like you and several others have pointed out. However, reversion has been noted in other situations (see citations in paper, and the post by Peter Gariaev), so that adds some credibility, even if their methods were not perfect.

Other than the authors’ suggestion, how could the allele revert from mutant to wild type? I agree, they didn’t screen broadly enough (or at least they didn’t show and discuss the data) for other silent mutations, and they don’t know the normal frequency of silent mutations in that gene. They also never looked at the non-reverted individuals to see if they had changed to nucleotides other than the mutant or revertant (ie. if there were non-reverting mutations at the point mutation). If there were (and if so, there would probably be other silent mutations), that would completely explain the entire problem.

I believe that we have to take things in the ‘high impact’ journals with a grain of salt - consider the papers claiming that hematopoietic stem cells (and other stem cell types) ‘transdifferentiated’ into functional mycoardium…this was later disproven when the recipient and donor mice each had distinguishable markers (GFP in one, lacZ in the other), showing that the HSCs were fusing with existing cardiomyocytes (Nygren JM, Jovinge S, Breitbach M, Sawen P, Roll W, Hescheler J, Taneera J, Fleischmann BK, Jacobsen SE. Bone marrow-derived hematopoietic cells generate cardiomyocytes at a low frequency through cell fusion, but not transdifferentiation.
Nat Med. 2004 May;10(5):494-501. Epub 2004 Apr 25.) (see paper for examples of the papers claiming transdifferentiation)

At the same time, we skeptic scientists have to open up our minds to possibilities that would necessitate rewriting textbooks. How many times has the model of the atom been changed? Don’t jump up and start rewriting now, wait until the theory has been proven, or disproven. But do be open.

Posted by Reed A. Cartwright on April 28, 2005 7:09 PM

Dana, I’m not a Dr., just a PhD student.

The wild type allele is the product of mutation. The system is more complicated than I first thought when I proposed fertility selection.

I think one of the functions of the hth gene is to break down an aromatic chemical that causes mutations. When hth is broken, this chemical builds up during some life stage and causes problem. I suspect that the life stage may be tied to pollen development, but I can’t say for sure without more knoweldege of the system.

Posted by Dana R-S on April 29, 2005 12:27 PM

I, also am a PhD student. I did my undergraduate work in plant genetics/plant breeding, and worked in canola breeding for several summers. I’m now working on developmental cardiac genetics.

I have read a bit of Petr Gariaev’s work, via a rough translation/abstract he supplied me with, and some figures with a bit of explanation. Essentially, the Russian work is suggesting that DNA has quantum mechanics-compatible qualitites - ie. electromagnetic signals, in addition to the actual nucleotide sequence. Like the Lolle et al work, this seems pretty far fetched, and I’m not at all familiar with quantum mechanics physics, so I really can’t evaluate the claim. But the idea behind it would suggest that the reversion events that Lolle et al are seeing would be due to this electromagnetic memory of what nucleotide should be in a particular position.

So this would be an alternate explanation to the RNA cache. I don’t know if it’s any more plausible than an RNA cache or mutation. Perhaps it’s more of a directed mutation.

Have you heard of the ‘wave genetics’ theory before? I’m hesitant to make much out of a topic when i can’t read the primary literature, as most of the early work seems to be in Russian. On the other side of the coin, there seems to be so many questions that we aren’t finding answers for by simply looking at the genetic code, and some of the answers we do find are completely unexpected. Perhaps we need another depth to DNA/genetics. I don’t know.

Posted by Dana R-S on April 29, 2005 5:51 PM

A note about the Lolle et al paper:

The chimaeric RNA-DNA oligonucleotide-mediated site-directed mutagenesis: papers have been rather torn apart in the literature. Can’t be replicated consistently, or can’t be replicated at all. See Science 298:2116 (The Strange Case of Chimeraplasty).

The comments on this article show up in a PubMed search, why would they cite something that has been discredited to that extent, and so obviously???

Posted by Leo Gao on June 25, 2005 8:04 PM

me, a phd student too. Have been discussing with buddies a lot on the paper. I guess many of us would propose selection model at a first glance but may hesitate doing so after a while. I am not really familiar with the field. However, what i wish to throw in here: recent progresses on RNA world may well remind us to be fully open-minded and prepared to embrace what might be astonishing or revolutionary. It seems the mother nature is way smarter than we have seen and is determined to surprise us again and again and again. At least central dogma is no longer as true as it was. By the way, I am currently hunting for a postdoc position and RNA world is one territory I like to explore. The more I read about the RNA world, the more I think this paper may be telling us something even though I would still be as surprised when follow-up tells us they were right! I’ll be watching on this and really look forward to follow-ups–true or false.

Posted by mike on May 28, 2007 1:23 AM

humm, i think its really the best paper and best narrations of this topic too.

Posted by mike on May 28, 2007 1:24 AM

humm, i think its really the best paper and best narrations of this topic too.