Late last year, Science published a bombshell - Lombardi et al's Detection of an infectious retrovirus, XMRV, in blood cells of patients with chronic fatigue syndrome. This paper reported the presence of a recently-discovered virus in 67% of the blood samples from 101 people with chronic fatigue syndrome (CFS).The question of whether people with CFS are suffering from an organic illness, or whether their condition is partially or entirely psychological in nature, is the Israel vs. Palestine of modern medicine - as a brief look at the Wikipedia talk pages will show. So when Lombardi et al linked CFS to xenotropic murine leukaemia virus-related virus (XMRV), they were hailed as heroes by some, less so by others. For some balanced coverage of this paper, see virology blog. Everyone agreed though that Lombardi et al was, as the saying goes, "important if true"...
But it wasn't, at least not everywhere, according to a paper out today in PLoS ONE: Erlwein et al's Failure to Detect the Novel Retrovirus XMRV in Chronic Fatigue Syndrome. The findings are all there in the title - unlike Lombardi et al, these researchers didn't find XMRV in the blood of any of their blood samples from 186 CFS patients.
Still, before people start proclaiming that the original finding has been "debunked", or decrying these results as flawed, some things to bear in mind...
This was a different country. Erlwein et al used patients attending the CFS clinic at King’s College Hospital, London, England. The patients in the original study were drawn from various parts of the USA. So the new results don't mean that the original findings were wrong, merely that they don't apply everywhere. Notably, XMRV has previously been detected in prostrate cancer cells from American patients, but not European ones, so geographic differences seem to be at work. So maybe XMRV does cause CFS, it's just that the virus doesn't exist in Europe, for whatever reason - but bear in mind that even the original study never showed causation, only a correlation. There are many viruses that infect people in certain parts of the world and don't cause illness.
On the other hand, it was a similar group of patients in terms of symptoms: Diagnosing CFS can be difficult, as there are no biological tests to confirm the condition, but Erlwein et al say that
Both studies use the widely accepted 1994 clinical case definition of CFS. Lombardi et al. reported that their cases ‘‘presented with severe disability’’ and we provide quantifiable evidence confirming high levels of disability in our subjects. Our subjects were also typical of those seen in secondary and tertiary care in other centres.But the first study selected patients with "immunological abnormalities", although we're given few details...
These are patients that have been seen in private medical practices, and their diagnosis of CFS is based upon prolonged disabling fatigue and the presence of cognitive deficits and reproducible immunological abnormalities. These included but were not limited to perturbations of the 2-5A synthetase/RNase L antiviral pathway, low natural killer cell cytotoxicity (as measured by standard diagnostic assays), and elevated cytokines particularly interleukin-6 and interleukin-8.The biological methods were similar: Both studies used a standard technique called nested PCR. (Lombardi et al also used various other methods, but their headline finding of XMRV in 67% of CFS patients vs just 4% of health people came from nested PCR.) PCR is a way of greatly increasing the amount of a certain sequence of DNA in a sample. If there's even a little bit to start with, you end up with lots. If there's none, you end up with none. It's easy to tell the difference between lots and none.
But there were some differences. The first study only looked at a certain kind of white blood cells, whereas the new study used DNA from whole blood. Also, the first study targeted a larger span of viral DNA - from 419 to 1154:
For identification of gag, 419F and 1154R were used as forward and reverse primers.Than the second one, which examined the section between positions 411 and 606. As a result, primer sequences used - which determine the DNA detected - were different. However, the authors of the new study claim that they would definitely have detected XMRV DNA if it had been there, because they used the same methods on control samples with the virus added, and got positive results...
The positive control was a dilution of a plasmid with a full-length XMRV (isolate VP62) insert, generously gifted by Dr R. Silverman.Silverman was one of the authors of the original paper - so hopefully, both research teams were studying the same virus. But (although I'm no virologist) it seems possible that the new study might have been unable to detect XMRV if the DNA sequence of the virus from British patients was differed at certain key ways - the whole point about nested PCR is that it's extremely specific.
Finally, there are stories behind these papers. The first study, that suggested that XMRV causes CFS, was conducted by the Whittemore Peterson Institute, who firmly believe that CFS is an organic disorder and who are now offering XMRV diagnostic tests to CFS patients. By contrast, the authors of the new study include Simon Wessely, a psychiatrist. Wessely is the most famous (or notorious) advocate of the idea that psychological factors are the key to CFS; he believes that it should be treated with psychotherapy.
I'm sure we'll be hearing a lot more about XMRV in the coming months, so stay tuned.
Erlwein, O., Kaye, S., McClure, M., Weber, J., Wills, G., Collier, D., Wessely, S., & Cleare, A. (2010). Failure to Detect the Novel Retrovirus XMRV in Chronic Fatigue Syndrome PLoS ONE, 5 (1) DOI: 10.1371/journal.pone.0008519Lombardi VC, Ruscetti FW, Das Gupta J, Pfost MA, Hagen KS, Peterson DL, Ruscetti SK, Bagni RK, Petrow-Sadowski C, Gold B, Dean M, Silverman RH, & Mikovits JA (2009). Detection of an infectious retrovirus, XMRV, in blood cells of patients with chronic fatigue syndrome. Science (New York, N.Y.), 326 (5952), 585-9 PMID: 19815723
30 comments:
It is likely that there will be a significant drop in sensitivity when using whole blood as compared to purified white blood cells. PCR may be a sensitive method to begin with, but sample preparation preceding the PCR is often more crucial than the PCR itself. Also if you look at the figures in the UK paper you can hardly see the positive control. I find the results in the US paper much more believable, but agree with you that there will be controversy. I am looking forward to more studies. Unlike you, I would not think that a single virus causing ME-like symptoms is a shock.
NeuroSkep:
Even though XMRV appears to be very genomically uniform for a retrovirus, a serious possibility here is a slightly divergent sequence on your side of the pond, in the sequence targeted by Wessely's primers. His paper does not employ techniques that might address this, such as touchdown PCR, degenerate primers, or simply trying for 5 or 6 different sequences in the XMRV genome instead of just one.
It would have been more convincing if Wessely had added serology into the mix, no? Fortunately, there are at least 15 labs working on this; we are going to hear more soon.
For what it's worth, the NK function deficit and RNase L oddity, though present in a number of the Mikovits/Lombardi subjects, were not correlated with the XMRV findings.
The 67% figure from the Mikovits paper certainly is widely reported. But Mikovits later reported to the media that 98% of subjects were positive when she used, on each of 100 CFS subjects, all four of the assays in the paper. This is yet unpublished. In the paper, PCR was applied to all subjects, but serology, viral culture, and viral protein expression were all applied to just a few.
I do not blame you for taking a neutral or reportage-like stance on this disease. But may I add, with honest hopes not to bore you completely, that I had thousands of very marked heart palps per day with this disease, sometimes 10-15 in a row. I also had rhinitis, but this is not easily distinguished from allergic rhinitis. (Though I have never had the latter to my knowledge.) Finally, I had petechiae in response to heat, and occasionally hives. My point is that various oddities often happen in us that are rather unlikely to be psychogenic. But generally none of them are common enough to make an impression in a study (with the possible exception of the rhinitis).
I was also just about bedridden with flu-like feelings, and suffering extreme symptoms which I wont go into -- I am now a great deal better than I was.
Anyway thx for your interest in this whole affair, and open mind. I do have my doubts, too -- not about the nature of the disease, but about the Mikovits/Lombardi paper, yeah. My confidence is around 50%.
Nils Reinton, thanks for your interesting comment. From the 'stract of one of the few (22?) papers on this virus, here be an instance of limited PCR sensitivity:
"We found XMRV DNA in 6% and XMRV protein expression in 23% of prostate cancers. [PMID: 19805305]"
Could this be the result of a SNP or two in some of the viral genomes? Maybe. I'm not sure how many total genomes we have, but I know Mikovits sequenced only three.
My GP once wondered whether I had CFS, but it turned out to be heart failure (idiopathic cardiomyopathy if memory, and spelling, serve). They never did identify which virus (or other wee beastie) caused it, but they didn't doubt that one did.
Hi, thanks for your interesting comment. Just one thing about patient selection. The WPI (US) study had patients meet the criteria for both Fukuda and Canadian Criteria. So the selection criteria was not exactly the same for both papers.
Some think Fukuda is too loose and could include people with milder, self-resolving, post-viral fatigue. The UK researchers were using banked samples, apparently, for this latest study, and Fukuda is that they had used for those earlier studies.
Anywway, I just thought I would mention it as there is some difference in the selection process.
I've heard that the subjects were "pretty sick" and mostly non-working. It would be hard for subject selection to explain the whole discordance of the two publications.
Using my HAM radio and ultra-sensitive seismograph (kidding), I am picking up rumors of further negative reports in the works. But as I said there are 15 or 17 groups in this little shootout, at minimum.
The Robert Koch-Institut in Berlin, essentially the German CDC, also reported negative (yet unpublished) findings on their website a few weeks ago. However this was taken down.
What I don't think has been remarked on here yet: that the amount of positives was zero in the Wessely paper. The Mikovits figure of 3.7% XMRV infection in the healthy control population is concordant with another report or two from studies of XMRV vis-a-vis prostate cancer.
Another little thing: in her publication Mikovits had only 50% positives using serology -- but she told the media (unpublished) that she had developed a better assay giving 95% positive serologies. She also stated (again unpublished) that she'd run unspecified assays (I would assume at least PCR + serology) in old London town -- and gotten the same numbers. Ergo, its very unlikely that geography alone can explain the Mikovits-Wessely discordance. Although, to repeat, one explanation would be that XMRV is geographical allelic in some primer sequences.
Thanks for the excellent comments all -
As Bitter CFS Jerk notes, the fact that Erlwein et al found no XMRV in 186 CFS patients is even more striking than it first appears given that, from Lombardini's results, you would expect to find 7 people with XMRV in 186 healthy controls. (3.7% of 186)
So even if Erlwein et al had selected people using completely different criteria to those used in the US, it is extremely unlikely that they'd have found no virus (I make the chance of it happening to be 0.963^186, or 0.0009.)
So it seems to me that there are only two options: either, XMRV does exist in Britain, but the Erlwein primers didn't detect it because of sequence variation in the "British strain" compared to the "American strain"
Or, the apparant presence of XMRV in the Lombardi samples was a mistake. Erlwein et al seem to be implying this with their closing paragraph:
Our own study also differs from that of Lombardi in other respects. Firstly, the PCR operator was blinded to the provenance of the DNA samples. In fact, with the exception of the PCR controls, all 186 DNA test samples originated from CFS patients. Care was taken to grow the XMRV plasmid in a laboratory in which no MLV had been cultured and no MLV vectors used and the PCR was carried out in a CPA-accredited Molecular Diagnostics Unit which processes only human tissue. Multiple (six) water (negative) controls were included in every run to detect low level contamination and a PCR to amplify a sequence that is conserved in most murine leukaemia viruses was included in order to expose any circulating MLV contamination and to detect any variant of XMRV that might be circulating in the UK CFS population.
Are there any other options?
Folks, with reference to my above post: my bad, the XMRV+ rate Wessely found in CFS probably isnt statistically significantly different from what was reported previously for healthy controls. Though it may differ from Lombardi/Mikovits' healthy control prevalence of 3.7%.
Below I quote the prior reports. I think there is also one more report on this from Japan, a conference poster or presentation -- I dont know the numbers on that one.
"XMRV sequences were detected in one of the 70 (1.42%) RNA samples from prostate tissue of healthy donors (Table 2)."
"we analyzed 233 consecutively accessioned prostate cancers and 101 cases of transurethral resection of the prostate (TURP) as benign controls (Fig. S1D). We detected XMRV DNA in 14 (6.2%) cases of prostate cancer and in 2 (2.0%) controls."
Actually there is one: someone, either in Erlwein or Lombardi's group, screwed up the PCR.
Neuro, pardon my priming you to focus only on the Mikovits/Lombardi healthy population prevalence. As penance I am now calculating p for Wessely's result as you did, but using the other two prevalence figures.
Good idea. Also, my figure assumes that the 3.7% is ground truth, whereas in fact it's subject to sampling error as well (with an n of just 101).
If I'm not mistaken, the chi-squared test does account for random sampling error (but not nonrandom sampling bias). But I'm a little outta my depth there.
I'm getting a slightly different p than you for 8/218 vs 0/186. I'm getting 0.0067 instead of 0.0009, using this calculator that belongs to a law firm; it runs the one-tailed Fisher exact test:
http://bardwellconsulting.com/statistical-significance-calculator
Using the figure from one paper, 2/100=2%... vs Wessely's 0/186:
p=0.121, not significant
For 1/70=1.4% vs Wessely's 0/186
p=0.273, anything but significant
And now... ladies and gentleman... the Wessely figure vs the aggregate of all three healthy population prevalence figures -- I hope (and do believe) that this is a statistically valid comparison to make:
11/388=2.8% (aggregated) vs Wessely's 0/186
p=0.01285, significant
So yeah, I think Wessely's result is unlikely to be consistent with the XMRV prevalence in normals, as reported in three earlier papers. *If* the thing is even found in England, etc.
To repeat, there is another such prevalence figure from Japan, unpublished, and I don't know what their number is.
I think the figure from the Japanese report is 1.75%, but I can't remember where I saw that.
Correction. From the Wessely paper itself:
"This follows an earlier claim that 1.7% (5/300) of healthy Japanese blood donors carried antibodies to the same virus [2]."
The footnote gives the full reference for the article.
(Well, I was close!)
Neuro, check out figs ein und zwei if you like. Hhmmmmmmm-mmmmmmmm...mmm, mmmmm; mmmmm. Arent those some awesome amplicons in fig 1? Indeed, Day-Glo.
Moving right along to numero deux, we note with some consternation that the amplicon from nested PCR positive control round one has a good deal more DNA than the one for round two, and is indeed looking pretty wan.
The thing really looks like hell.
I do have my doubts about the Big Paper -- but, the thing is, the PCRs were confirmed even before it was published by the National Cancer Institute and the Cleveland Clinic. Those are two mighty big fish on the american scene.
Thanks anon. I missed that. For my aggregated calculation, this would not move the mean prevalence much. But it adds a great deal to the sample size, moving p still lower. One wonders why this japanese thing isnt in print. It is not exactly a sleep-inducing finding.
"Actually there is one: someone, either in Erlwein or Lombardi's group, screwed up the PCR."
http://www.wpinstitute.org/news/docs/WPI_Erlwein_010610.pdf
"1) blood sample volumes and processing;
2) patient criteria/population differences;
3) number and type of tests done to assure accurate results, including white blood cell
culture;
4) use of a molecular plasmid control in water versus a positive blood sample; and
5) different primer sequences and amplification protocol used to find the virus, which
were not validated by a clinical control."
In addition, the response says:
"Significant and critical questions remain as to the status of patient samples used in the UK study as those samples may have been confused with fatigued psychiatric patients, since the UK has relegated 'CFS' patients to psychiatric care and not traditional medical practices."
With Cleare and Wessely involved in this paper you can gaurantee patients are less likely to meet the objective, testable criteria of the 2003 Canadian definition.
"I've heard that the subjects were "pretty sick" and mostly non-working. It would be hard for subject selection to explain the whole discordance of the two publications."
Unfortunately that in itself doesn't mean much as far as diagnosis goes as it's inferred this is self-reported "sickness" and not something objectively measured with a tilt table test, bicycle ergonometry or whatever.
The sort of testing that is not carried out within the NHS for people with ME/CFS.
The failure to use accurate, distinguishing criteria has dogged CFS research for the last twenty years and encouraged the fatalism of artificaly inflated "heterogeneity", allowing for dissembling among academics and policy makers and ensuring a serious disease remains forever in the twilight of "negativity": negative findings, negative significance, negative signs, negative definitions, negative disability, negative communication between researchers, negative rapport, negative understanding, negative press, negative support, respect, and hope. But here's the panacea of CBT to jolly it all up regardless. Why should things change now?
All very interesting but doctors need to properly rule out Lyme disease before making a ME/CFS diagnosis something that is clearly not happening at present.
My 6 1/2 year illness diagnosed as Figromyalgia and then ME/CFS responded to a chance course of antibiotics and eventually led my doctors to realise it was actually Lyme Disease.
With the controversy over diagnosis testing and treatment is it any wonder that 75% of people being diagnosed with Lyme disease previously had an ME/CFS diagnosis.
see http://www.ilads.org/ for more details and UK charity
http://www.lymediseaseaction.org.uk/
Anonymous: I can well believe that CFS diagnosis is a shambles. I don't know much about that, but diagnosis of psychiatric disorders, my area of interest, is also a shambles & probably underlies a lot of the negative results or inconsistency in this field.
However, I don't think diagnosis can explain the Wessely results because Wessely found no XMRV in any of 186 "CFS" patients - implying, basically, that no-one who attends the King's College CFS clinic has CFS according to the criteria Lombardi et al used.
If Wessely found that only say 25% of his sample had XMRV I'd start asking questions about diagnosis, as it is, I think that can't be the only thing going on here.
Neuro, Many a def there be. Most are more or less reasonable -- certainly, at least, for purposes of study and surveillance.
There is one def we all loathe and that is the one of Reeves, CDC's head of CFS. Population-based point prevalences of CFS are:
0.235 ("CDC mark one", I think) 0.422 (Leonard Jason).
Reeves, using his divergent "empirical def", finds a point prevalence of 2.45%, or 5.8x higher than Jason's work!
The Reeves def has not been adopted very much by other workers, which doesn't exactly break our hearts. We basically consider it war on our faint (recently not so faint) hopes of biological resurrection.
It is interesting that three of the psychiatrists in the failed UK study have adamantly insisted that CFS is a psychosomatic disorder for more than 20 years now. (The unofficial term they use is functional somatic syndrome.)
Dr. Wessely would appear to have much to lose if CFS patients have XMRV or any other viral process and the biological abnormalities other CFS experts have found in well characterized subgroups.
(Correct me if I'm wrong, but in psychiatry if there is a possible medical explanation for the signs and symptoms then it cannot be labled as psychosomatic. (And the symptoms of CFS, watered down as they may be, are still common symptoms of an infectious process. Severity and duration are usually key to a differential diagnosis.)
Although it is my understanding that Sharpe and company are now trying to change that so that a person can be diagnosed with a organic disease and a psychosomatic disorder at the same time.)
Someone else pointed out that the patients in the UK study were different from the Lombardi group because they didn't appear to meet the 2003 Canadian Consensus Definition. http://www.cfids-cab.org/cfs-inform/CFS.case.def/carruthers.etal03.txt
Of course not - you can't meet that definition and have a functional somatic syndrome.
I think Dr. Wessely's own words sum up his actual position rather well,"...indeed, the search for infective causes and triggers for psychiatric disorders has never ceased..."
(Factual note: Although Dr. Wessely refers to CFS in his essay - the CFS, along with PVFS and ME, are listed by the WHO since 1992 under the ICD-10 G93.3 as an organic brain disease and are specifically excluded from a psychiatric listing under F48 - a fact he fails to mention.)
"...it is clear that the drive to find a somatic biomarker for chronic fatigue syndrome is driven not so much by a dispassionate thirst for knowledge but more by an overwhelming desire to get rid of the psychiatrists."
Wessely S (2009). Surgery for the treatment of mental illness: the need to test untested theories. James Lind Library (http://www.jameslindlibrary.org).
Remind me what the DSM-IV definition of paranoia is? ;D
More seriously I agree with Dr. Silverman in that everyone should be wary of hasty studies following Lombardi et al regardless of the results. As noted all over the blogosphere, right now everyone uses their own protocol which makes studies interesting and possibly informative, but not necessarily replicative. Still a long way to go.
KAL,
The symptoms aren't exactly watered down in general, though they do range all the way to mild.
I guess you have a point, about the non-febrility. That much is certainly pretty tame looking compared to many infections.
But there are people that regularly crawl to get to the bathroom.
When I was very sick (for about 18 months) it was like the "flu" most days. I don't know, of course, whether I have ever had influenza, but what I had was like a flu in the colloquial sense. Fine food tasted like sawdust. At times I couldn't sit up long. But the mental dysphoric states were worse. What terrible nausea is to the stomach, is what every perception and thought was like to my psyche. I couldn't stop thinking and have a blank mind for 3 or 4 seconds, which is something much more important than one may realize -- there was a drive that kept me thinking, verbally, all the time, literally 100% of the time. It took tremendous effort to focus my attention away from the default topic, which was suicide, bleeding, etc. I did not have the power to exert so much attention, so each day I would burn out quite soon and be unable to prevent myself from sitting and thinking about suicide for 6 or 8 hours. (I could never bear watching TV, and often couldn't read very much.) Whenever I saw my wrists I imagined opening my veins, unable to repress it.
So, its just a basic encephalitis, when its severe like that. (At least, this is very likely. There is no definite objective encephalitic finding, though evidence consistent with modest brain inflammation was obtained by a group at Georgetown.) I know, there are certainly worse encephalitides, psychotic ones. But this was absolutely spectacular. I can't convey what it was like. It was like being drunk, wasted, only having drunk poison instead of wine.
I am far better now -- what I have now is like a very watered-down cold, and so I have been for many years.
Anyway, I'm not sure the nature of symptoms helps you distinguish physiogenic from psychogenic diseases. It seems unclear to me, anyway, that psychogenic diseases exist, though I know little about anorexia nervosa or PTSD and they seem like plausible examples. However we can note that the latter is associated with extreme trauma, and is in that way no mystery. It seems quite possible that chronic depression is physiogenic. Recall that shcizophrenia was once thought psychogenic. There still seems not to be overwhelming evidence that it isn't, but the idea that it is has come to seem sort of silly. Perhaps because the neurotogenesis schools of multiple entities like migraine and narcolepsy have been blown to heck.
Also, it would not seem likely that symptoms alone can distinguish between infection and autoimmmune disease.
The idea that all conceivable physical causes of a disease entity could be ruled out in a good vintage 1960, 1980, 2000 biomed reserach lab, particularly a brain disease for heaven's sake, never had the least intelligence to it at all. It was absolute hubris. It was even nuttier in the 1930s, but that didn't stop psychogenesis from flourishing then, in narcolepsy and in other disease entities where it was soon to be routed. This shows us something we should remember: that erudite humans like to play around with psychogenesis like a bauble, and will.
KAL: "Correct me if I'm wrong, but in psychiatry if there is a possible medical explanation for the signs and symptoms then it cannot be labled as psychosomatic."
Not exactly. Psychiatrists would define symptoms as psychosomatic if they were apparently not caused by an organic pathology in any given case. There are many syndromes which can be organic, but which can also be "psychosomatic" i.e. associated with no evident pathology. Pain, paralysis, and seizures, for example, can be organic but can also be "psychosomatic".
What I find most odd about the CFS debate is that most of the people who believe CFS is psychosomatic are psychiatrists - psychiatric disorders being, almost by definition, disorders without a clear organic pathology, yet few psychiatrists would admit that depression or schizophrenia were psychosomatic! They would say that they were brain diseases with an as-yet-unknown pathology.
I don't know if Simon Wessely would agree with that, but that's psychiatric orthodoxy regarding psychiatric disorders. Yet for some reason no-one seems willing to admit CFS to the exclusive club of "we know it's organic and we'll get back to you when we know exactly how" diseases.
What's funny is that there seems to be no overwhelming evidence that depression is organic. (I'm not saying I think it is non-organic.)
"Psychosomatic" seizures are interesting. There I am stymied again in trying to understand the thinking. What exactly leads us to think a person cannot convulse involuntarily and have an altered level of awareness without ictal activity? I think its indisputable that such convulsion is possible a priori: if I lie in bed and intentionally thrash around, I don't show an epileptiform EEG.
The thing is it's just hard to imagine why this would happen involuntarily without disordered activity in the brain -- why would an extreme few neural paths be activated improperly when others aren't? Well, my question is, why is epileptiform EEG the only measure of any possible disordered neural firing? According to the sparse neural coding hypothesis it takes "very little" to "do things" in the brain, in other words the firing of a single neuron may produce an effect on behavior or consciousness. So why can't you have a cryptic seizure? Dysregulated firing that's 1000x less disordered than the epileptic state might still be extremely disordered.
I realize that there's also a placebo/nocebo/call-it-whatever issue in "psychogenic" seizures, wherein the seizures are suggestible: placing a colored patch on the subject's skin can induce the seizure state if a doctor tells the patient that it probably will. I don't see this as fatal to the possibility of this being an organic disorder. When I read a patient forum on this, many seemed to find their seizure experiences dysphoric, so I think that anticipating the onset of one could potentially cause arousal and anxiety that could cause the seizure.
It seems quite possible to me that the whole things has been misinterpreted.
Hi Neuroskeptic -
Interesting.
Based on an extensive reading of his research and remarks, Dr. Wessely does not appear to be big on any “bio” unless it fits with his professional interests. He has devoted most of his 20+ career to proving his interpretation of psychiatrist George Engel’s biopsychosocial theory using diseases that were classified as organic diseases not psychiatric disorders prior to his entry into the field as examples. And most remain classified by organizations such as the WHO as organic diseases despite his best efforts to change them. Dr. Wessely rarely points out that his viewpoint is often at odds with both his peers and well known and well regarded biomedical experts. Perhaps patients are easier to marginalize. I don’t know his intent – I’m not him. I can only observe his chosen actions.
PubMed contains a solid level of evidence of all kinds of organic pathology abnormalities in patients with CFS or perhaps I should say subgroups. The Cliff Notes version can be found here. www.cfids.org/about/10-discoveries.pdf
It is quite possible that by broadening the case definition over the years since Dr. Melvin Ramsay's time and changing the name to something far more generic it may have artificially moved CFS to a more heterogeneous grouping. It could be many diseases under one name with core symptoms in common or mixed in patients who are depressed and tired, but would not have fit earlier less broad inclusive definitions.
By deleting neurological signs such as a positive Romberg which CFS expert and Neurologist Ben Natelson consistently finds in most of his CFS patients and diluting say pathological exercise tolerance to mere tiredness it fits more closely with the psychosomatic viewpoint, but is it accurate? Using the same term for two entirely different groups of people could be considered problematic.
Some of Dr. Wessely’s peers have done research showing that such a move may have added in many people who do not have CFS at all, but who do have psychiatric disorders. US psychologist Leonard Jason who has been on countless definition committees and groups has addressed this many times – check PubMed. One of the most recent is:
Jason, LA, Najar N, Porter N, Reh C. Evaluating the Centers for Disease Control's empirical chronic fatigue syndrome case definition. Journal of Disability Policy Studies 2008, doi: 10.1177/1044207308325995.
Further reading can be found on the website of the largest international group of CFS professionals: clinicians, biomedical and behavioral researchers, and educators comprise the IACFS.
Leonard Jason, Ph.D., DePaul University. Problems with the New CDC CFS Prevalence Estimates
http://www.iacfsme.org/IssueswithCDCEmpiricalCaseDefinitionandPrev/tabid/105/Default.aspx
Also check the pedigree of the vast majority of the members of International Chronic Fatigue Syndrome Study Group and you won't find many virologists or other biomedical researchers for example. This could also account for the increasing heterogeneity of the population grouped under this umbrella.
Good conversation. Thanks
Hello friends -
I've read a few things that cause me to question the England study:
1) It was in peer review for three days, as compared to six months for the WPI paper.
2) There were some rather large discrepancies between patient groups:
"Patient samples. Banked samples were selected for this study from patients fulfilling the 1994 CDC Fukuda Criteria for Chronic Fatigue Syndrome (S1) and the 2003 Canadian Consensus Criteria for Chronic Fatigue Syndrome/myalgic encephalomyelitis (CFS/ME) and presenting with severe disability. Samples were selected from several regions of the United States where outbreaks of CFS had been documented (S2). These are patients that have been seen in private medical practices, and their diagnosis of CFS is based upon prolonged disabling fatigue and the presence of cognitive deficits and reproducible immunological abnormalities. These included but were not limited to perturbations of the 2-5A synthetase/RNase L antiviral pathway, low natural killer cell cytotoxicity (as measured by standard diagnostic assays), and elevated cytokines particularly interleukin-6 and interleukin-8. In addition to these immunological abnormalities, the patients characteristically demonstrated impaired exercise performance with extremely low VO2 max measured on stress testing. The patients had been seen over a prolonged period of time and multiple longitudinal observations of the clinical and laboratory abnormalities had been documented."
Here is the UK study patient selection:
"All patients had undergone medical screening to exclude detectable organic illness, including a minimum of physical examination, urinalysis, full blood count, urea and electrolytes, thyroid function tests, liver function tests, 9 a.m. cortisol and ESR. Patients were interviewed using a semi-structured interview for CFS [9] to determine whether they met international consensus criteria for CFS. All subjects met the CDC criteria [10]; patients with the Fukuda-specified exclusionary psychiatric disorders, or somatisation disorder (as per DSM-IV), were not included."
Thanks to Smurf @ In the Pipeline for this analysis. I'm just stealing, but thought that others might find his analysis of interest. As he so brilliantly stated, comparing these two groups together is like comparing smurf and smurf.
Also of potential interest is that reference 9 in the England paper was for diagnostic purposes was a paper written by the same author.
- pD
"All patients had undergone medical screening to exclude detectable organic illness, including a minimum of physical examination, urinalysis, full blood count, urea and electrolytes, thyroid function tests, liver function tests, 9 a.m. cortisol and ESR. Patients were interviewed using a semi-structured interview for CFS [9] to determine whether they met international consensus criteria for CFS."
A patient of Dr Wessesly who took part in his XMRV study commented online saying that this was untrue and that he had not been screened for any other condition by Wessely.
Look at the other Plos one comments for further criticisms of the patient population issue. In the IC study, patients were selected FROM 'consecutive' attenders, and that could only happen if the patients were screened out for organic abnormalities first. A VERY deliberate selection process, and different to the WPI cohort.
Also look at the 'disability' issue. At least one comment has mentioned that.
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