We appreciate the opportunity to address some of the criticisms of our paper (Byrnes et al., PLoS One 2009;4(6):e5805).

1. Drs Vernon and Kerr criticized our case definition (chronic fatigue syndrome plus idiopathic chronic fatigue, CFS and ICF). First, this issue is not as simple as the authors make it out to be as considerable controversy and substantial difficulties about how to define CFS persist. Second, we have described the epidemiological and genetic epidemiological rationale for our preferred definition of illness elsewhere (PMIDs 16168154, 16168155, and 16168156). These conclusions were based on large-scale, population-based samples. Third, we believe Dr Kerr to be incorrect as our diagnostic criteria for “chronic fatigue (i.e., CFS and ICF) are indicated in the paper (Methods, paragraphs 2-4).

Finally, and most importantly, the case definition criticism is rendered invalid as we did analyze the CFS definition favored by Drs Kerr and Vernon. Our paper had three definitions of affection, one of which included only subjects with clinically-evaluated CFS per standard criteria. Thus, for all definitions of illness ranging from the one we favor to the standard definition, there were no differences in PBL gene expression between affected and unaffected monozygotic twins.

2. Dr Vernon criticizes our scholarship on the grounds of neglecting to mention “more than 50 publications” of gene expression in CFS. Closer inspection of these 51 PubMed hits (“gene expression” and “chronic fatigue syndrome”, 23 July 2009) reveal a number of review articles and papers not immediately relevant to our case-control study (e.g., studies of gene expression in subsets of CFS cases). We note that our statement in the second paragraph of the introduction reads: “We are aware of four published non-overlapping studies that compared gene expression in PBLs in cases with CFS *in comparison to controls*” (emphasis added).

3. We are puzzled by Dr Kerr’s main comment: “The biggest weakness in the paper is that the SF36 scores for the patients versus controls were not particularly different … a t-test would have been useful, but I suspect that this would reveal these 2 populations were not statistically different”. First, the sixth and seventh lines of Table 1 present paired t-tests contrasting affected and unaffected twins and, contrary to Dr Kerr’s statement, there were substantial and significant differences in the expected directions (p=0.004 and p=1e-5). Second, in regard to the status of the unaffected twins, we stated in the Results (paragraph 1) that “the mean functioning of affected twins was over a standard deviation worse than Swedish norms whereas the unaffected twins were similar to Swedish norms”. Thus, Dr Kerr’s criticism is inconsistent with the content of our paper.

4. Dr Kerr criticized our choice of transcripts studied for verification using qRT-PCR. These transcripts were mostly based on our empirical findings (i.e., genes with the smallest although non-significant p-values) and from the literature (e.g., DCTN1 was from Dr Vernon’s 2002 paper). None was significantly different between affected and unaffected monozygotic twins.

5. Dr Vernon correctly points out that globin mRNA can be expected to reduce the sensitivity of the Affymetrix U133 gene expression assays. When this experiment was conducted in 2006, we were aware of this issue and spent considerable effort testing globin reduction protocols provided by Affymetrix and with several modifications (e.g., using PNAs instead of DNA oligos). None provided satisfactory results and so we proceeded in the manner described in the paper. We rejected the use of methods to select sub-populations of cells given the risk of such manipulations altering gene expression. Note that the scientists involved in this work, and the subsequent array processing, had at that time several years experience of performing gene expression profiling experiments using the Affymetrix platform and were very familiar with the various protocols.

The implications of our informed choice of protocol are likely different from what Dr Vernon asserts. While there may have been a reduction in sensitivity, it cannot explain several aspects of our study. First, if there truly are robust and reproducible differences in gene expression that characterize CFS, why are these not seen in most studies? Second, some loss of sensitivity cannot explain our non-significant results – particularly given the negative results of the qRT-PCR assays which should not be influenced by globin levels.

Third, we have conducted genome-wide association genotyping on these samples (manuscript in preparation). We find many strongly significant and reproducible SNP-transcript associations that match those reported in other samples by other groups. If our expression data were as flawed as Dr Vernon asserts, no such associations should have been observed.

We reiterate our conclusions: (a) We attempted to correct methodological issues in prior reports by careful control of sources of bias (e.g., by studying discordant monozygotic twin pairs, use of RNA stabilizing media, and standardized sampling conditions). (b) We found no evidence of differential PBL gene expression that characterized the presence or absence of CFS or ICF. We believe that these conclusions are not altered by the criticisms of Drs Vernon and Kerr.

The possibility that the positive findings of prior studies were due to methodological artifacts has not been excluded.