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Said-Nahal and colleagues report an intriguing finding of an association with HLA-DR4 independent of B27 in families with ankylosing spondylitis (AS),1 a finding highlighted by an accompanying editorial.2 The approach of studying B27 positive and B27 negative haplotypes may prove powerful in identifying further cis or trans encoded genes involved in AS. However, the reported association of DR4 with AS is quite a surprising finding given that no difference was noted in B27-DR4 haplotype frequencies in patients and ethnically matched healthy controls. Many previous studies have not reported any such association,3–9 including a similar preliminary study by the same authors.10 Although these studies were mainly case-control studies, population stratification is highly unlikely to cause a false negative finding if the effect size of the reported association with DR4 is as high as Said-Nahal and colleagues describe.
We are concerned that both the family and case-control results are biased by the statistical approach employed. Multicase families were used in the study, yet a form of transmission test for linkage disequilibrium (TDT) was used11 which is only suitable for single affected families, and is a valid test only of linkage, and not of association, when applied to multicase families.12 Therefore the TDT p values reported in tables 5, 6, and 7 of Said-Nahal's paper1 for the patients and unaffected B27+siblings do not reflect association alone, and will be affected by the strong linkage of the major histocompatibility complex with AS, and also probably by bias due to the different numbers of parent-case trios selected from different multicase families. Forms of TDT are available for general pedigree families and are more powerful than the TDT employed in this study (for example, see Clayton13). These biases also apply to the case-control component of the study (results presented in tables 2, 3, and 4) where it appears that related cases were employed. If so, these results also reflect both linkage and association. We would be interested to see the results of a further analysis allowing for these considerations.
Both MAB and AMC are supported by the Arthritis Research Campaign (UK).
We thank Dr Brown and colleagues for their interest in our recent publication.1 In their comment, they raise a number of questions which we have tried to address. The reported effect of HLA-DR4 appears to be independent of linkage with HLA-B27, meaning that it is not accounted for by linkage disequilibrium with HLA-B27. However, this observation does not necessarily imply that it is independent of HLA-B27, considering that HLA-B27 was almost constant among patients with familial spondyloarthropathy (SpA) (in other words, the DR4 effect may combine with the B27 effect, rather than being truly independent).
In our study the presence of DR4 increased the risk of developing SpA among HLA-B27+ siblings (odds ratio = 2.8, 95% confidence interval 1.4 to 5.7), which is far less than the effect of HLA-B27. This result is based on HLA-DRB1 typing of 185 patients and of 71 healthy siblings. Only one of the previous association studies cited by Brown and colleagues had comparable sample size.2 Even in that study, however, no more than two thirds of the patients belonged to multiplex families and their controls were from the general population. The DR4 effect may be specific for familial disease, requiring the use of healthy siblings from multiplex families as B27+ controls, to demonstrate an association. Given these considerations, previous studies cited by Brown and colleagues were presumably underpowered to detect a DR4 effect. This was obviously the case with our preliminary report analysis3 which concerned only 13 of the 70 multiplex families included in the present publication.
We used Spielman's transmission disequilibrium test (TDT) to examine whether the transmission of HLA alleles to patients differed from random.4 As opposed to association studies, these statistics are not exposed to population stratification bias. Yet, it was originally designed to test the transmission of biallelic markers in single families, and we agree with Brown and colleagues that its results in multiplex families need to be interpreted with caution. Hence linkage of the disease examined with a locus in a region might interfere with the results of a TDT applied to another locus in the same region, which might wrongly be interpreted as evidence for meaningful association with particular markers. In the specific case of HLA region such risk is even present when using single-affected families because of the strong linkage disequilibrium between alleles at separate loci. Such bias is notably illustrated in our study by the influence of linkage disequilibrium with HLA-B27, which affected the transmission of several alleles at HLA-A, C, and DR loci, when studying all haplotypes together. However, when the analysis was confined to the non-B27 haplotypes, all these alleles appeared to be randomly transmitted, except for HLA-DR4. Such unique disequilibrium strongly suggested that HLA-DR4 itself contributed to SpA predisposition, albeit as already discussed in our publication, we could not entirely rule out that it was secondary to a preferential association between SpA and another major histocompatibility complex gene.
Additional studies will clearly be needed to confirm our results. However, according to our present data, we would have needed to type 50 more multiplex families to reach a power sufficient to demonstrate a DR4 effect, by using statistics developed for general pedigree families as suggested by Brown and colleagues.5
Finally, regarding the case-control component of the study, we disagree with Brown and colleagues that our results reflected both linkage and association, because any HLA-B27 haplotype identified in a family was counted only once, even if present in several patients.
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