Rudrasingham V, Wavrant-De Vrièze F, Lambert JC, Chakraverty S, Kehoe P, Crook R, Amouyel P, Wu W, Rice F, Pérez-Tur J, Frigard B, Morris JC, Carty S, Petersen R, Cottel D, Tunstall N, Holmans P, Lovestone S, Chartier-Harlin MC, Goate A, Hardy J, Owen MJ, Williams J.
Alpha-2 macroglobulin gene and Alzheimer disease.
Nat Genet. 1999 May;22(1):17-9; author reply 21-2.
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Response from Allen Roses et al. to Tanzi Comment
Below please find a short, absolute rebuttal to the comments made by Rudy Tanzi. It is followed by a fairly detailed commentary on each point, including copies of relevant dated correspondence that clarify the facts. Despite the claims and exhortations proposed to support an association of AD and an alpha-2-macroglobulin polymorphism, the evidence from multiple laboratories provides no support for the association. Scientists should expect robust confirmations to be clear and universal, as with the association of APOE4 with AD, especially when statements referring to a stronger effect of A2M are part of the publicity. A careful reading of the information attached will clarify the data, the effect of Dr. Tanzi's commercial conflict of interest, and his clear deviation from facts.
I should point out that I have had a clear academic, and now a commercial, interest in the therapy of AD. We have no commercial or academic interest in the non-association of A2M with AD. It is now confirmed that a second susceptibility locus for AD is located on chromosome 12, but A2M is simply not it.
Allen D. Roses, M.D.
Vice-President and World-Wide Director, Genetics
Co-Chair, Exploratory Discovery Board
Glaxo Wellcome R&D
Correspondence submitted by: Jonathan Haines, Margaret Pericak-Vance, Lindsay Farrar, Bill Scott, Ann Saunders, Peter St George-Hyslop, and Allen Roses
Dr. Tanzi raises a litany of concerns in his commentaries starting 5/13/99. As summarized in the following two paragraphs, and as described in more detail in the subsequent paragraphs, his arguments are logically or factually weak and his comments sometimes inappropriate.
Dr. Tanzi implies that adding non-significant results to significant results, and then still getting a (much less) significant result constitutes independent replication. This is obviously not true. Dr. Tanzi also implies that the family-based studies of Rogaeva et al. are hampered by small sample size, when in fact the sample sizes (105 total non-NIMH families, 143 NIMH families) are both equivalent to or larger than that used in his own original study (102 NIMH families). Dr. Tanzi implies that linkage to a broad region of chromosome 12 indicts specifically A2M, when in fact it indicts all genes in that region. Dr. Tanzi seeks support from the Val1000Ile study he performed in a case-control series. However, this result was marginal, has not been confirmed in other datasets (including the NIMH family dataset), and the A2M-2 result was not seen in his case-control dataset. Thus, far from supporting his assertions, a full accounting of the data raises even more doubt. Dr. Tanzi neglects to mention the fact that the A2M-2 allele has no biological effect. Dr. Tanzi has been fully aware for four months that the genotypes generated in his lab and in our labs are 96% concordant, and that genotyping discrepancies cannot explain the difference in the results between the two datasets. The only valid explanation of the difference is that the original result is not robust and does not replicate when applied to additional families from the NIMH collection. Finally, Dr. Tanzi has not fully declared his potential conflict of interest in this matter. On March 2nd, one day before our paper received its final acceptance (and after four months of review primarily to answer Dr. Tanzi's concerns), Genoplex, Inc. announced an exclusive deal with Dr. Tanzi for rights to the A2M results.
We have elected to reply to his comments in order to rectify, for the scientific community, the misleading and sometimes-erroneous statements contained in Dr Tanzi's commentaries. However, we would state up front that we have no interest in further perseveration on this discussion. The issues are really very clear! We believe that our four independent data sets, re-evaluation of an enlarged subset of the NIMH data set (the one studied by Tanzi and colleagues), and expression and protein studies of the A2M insertion-deletion polymorphism, as well as the studies of Dow et al and Rudrasingham et al, in the aggregate provide compelling evidence against an association between AD and A2M. However, we understand how this high-profile controversy may prompt other groups to publish their results. As in all purported gene associations, the burden of proof rests on repeated positive results in independent data sets and the demonstration of an effect of the polymorphism on biological activity.
The detailed comments to Dr. Tanzi's statements are below:
Dr. Tanzi writes: "Rudrasingham et al.... not only confirmed our report of family-based association of A2M and AD in the NIMH families, but they also observed a positive trend in the same direction in an independent albeit smaller set of families (the NIA set). This observation serves as an independent corroboration of our original report of family-based association between A2M and AD."
The p value reported by Rudrasingham for their NIA set was 0.1. Most would not regard p = 0.1 as statistically significant, and it certainly does not qualify as an independent confirmation of a controversial result which cannot even be replicated in the original dataset by a separate group of investigators. Likewise, adding the results of the NIMH samples tested by Blacker et al (and re-tested by Rudrasingham) to the new (but non-significant) results from the NIA set tested by Rudrasingham generates a p-value which, in truth, is much less significant than in the NIMH set alone! This also does not constitute independent confirmation - in fact quite the converse!
Dr. Tanzi writes: "It may be worth noting that some of the authors on the Rogaeva et al paper recently reported that by genetic linkage analysis using DNA markers, maximum evidence for linkage to AD was found at marker D12S358 which resides very close to A2M (JAMA, 1999). Thus, traditional genetic linkage findings from numerous groups implicate the telomeric region of the short arm of chromosome 12 directly near A2M (in contrast to the original linkage findings reported by Duke in 1997, which placed the chromosome 12 AD-associated gene much closer to the centromeric region of the chromosome.)
There are several errors here both in the logic and in the facts. First, although we agree that positive linkage results near A2M initially suggested A2M as a candidate susceptibility gene, linkage also implicates all other genes in that broad region of the chromosome. A2M has now been directly tested and is not associated with AD in the same families that gave the positive evidence for linkage. The original genetic linkage studies of Pericak-Vance et al. (JAMA, 1997) and the follow-up linkage studies of Rogaeva et al (JAMA, 1998) and Scott et al (JAMA, 1999) in fact implicate a very broad region of chromosome 12 (~67 cM). These papers clearly state that no statistically significant preference for any given location can be made. As others have pointed out (Craddock & Lendon, Lancet, 352:1720-1721, 1998), linkage analyses in complex traits with multiple small pedigrees typically gives weakly positive scores, which poorly localize the defect. It is inappropriate to selectively seize upon one region because it has a marginally (but not significantly) higher lod score under only one of several methods of linkage analyses. It is also naive to believe that linkage analysis in complex traits can implicate only one gene within a broad interval. Thus declaring that A2M, falling within the general vicinity of that "peak", must contain genetic variants associated with susceptibility to AD is obviously incorrect.
Dr. Tanzi writes: "I think the most important point is that two of the three groups who have explored this issue (ours and Rudrasingham et al.) have observed significant family-based association between A2M and AD (while Rogaeva et al report marginally significant findings for the NIMH set). This fact, together with the report of positive case-control studies from Brad Hyman along with the association of an A2M variant with increased amyloid deposition, multiple reports of strong genetic linkage between AD and markers in the A2M region of chromosome 12, and the demonstrated role of A2M in A-beta clearance and degradation suggest that the role of A2M in AD merits further study...."
The pretzel is getting rather twisted. Again, this statement is flawed both logically (containing a mix of facts, wishful thinking, and hypothesis) and factually. First, as we have pointed out, the non-NIMH data of Rudrasingham et al and Rogaeva et al do not show a statistically significant association. Second, the study of the Val1000Ile polymorphism by Hyman/Tanzi et al used a case-control, not a family-based, design. Dr. Tanzi has consistently stated elsewhere that an A2M-2 effect cannot be detected in sporadic AD because of something special about the biology of the A2M/AD association. Third, the Hyman/Tanzi et al. result was very marginal and certainly is not an indication of the strong genetic effect originally proposed by Tanzi. Fourth, no mention is made of the fact that the Val1000Ile polymorphism is not associated with AD in the NIMH dataset, and the A2M-2 polymorphism is not associated with sporadic AD in the Hyman/Tanzi case-control data set. Also not mentioned is the fact that other studies of the A2M Val1000Ile polymorphism have either found a disease association with the allele reported to be "protective" in the Hyman/Tanzi data set (Myllykangas et al, Ann. Neurol, 1999) or no association at all (e.g. Wavrant-DeVrieze et al., Neurosci Lett, 1999). At the very best, these conflicting association studies might cumulatively implicate linkage disequilibrium with some other gene in this region. More plausibly, it's simply the same old noise that's repeatedly seen in case-control studies in human populations with a variety of different diseases (it's not peculiar to AD). Finally, A2M may well have a biological role in the clearance of Abeta (but even here not all agree). However, that A2M may or may not have a role in Abeta clearance (or even in AD pathogenesis) neither requires nor supports the notion that genetic variants in A2M must have any effect on susceptibility to AD.
Surprisingly, in this long list of comments, Dr. Tanzi consistently omits discussion of any substantial evidence of a biological effect of the A2M-2 variant. In fact, as described in the Rogaeva paper, there is no evidence that the A2M-2 variant has any affect on A2M mRNA or protein in brain, liver or plasma. We will pre-empt here some of the speculative explanations that we have heard at various meetings. The A2M-2 splice variant doesn't affect "the 11 base upstream polypyrimidine tract" which potentially modulates RNA splicing. The A2M-2 does not cause "production of a small amount of truncated A2M monomers which are selectively retained in the endoplasmic reticulum but which affect A2M multimers" (no truncated monomers are detected in brain homogenates even in A2M-2 homozygotes). However, even if it did, these "truncated monomers" would not be available to affect extracellular activity, which is where Tanzi believes A2M acts in the pathogenesis of AD. "Diet and diurnal variations" have little effect on A2M plasma levels.
Dr. Tanzi writes: "Regarding the discrepant p-values reported by our group and by Rogaeva et al for family based association of A2M and AD, we need to analyze our respective genotypes for the NIMH set side by side to resolve the difference. For example, it is possible that the family material distributed to each site and the exact family members that were genotyped differed or there were differences in the genotypes obtained."
The discrepant results are due to a Type I error in the original report. Enlargement of the data set (from the original 102 families used in the Tanzi analysis to the 143 used in our analysis) was done using families drawn by the same investigators from the same populations using the same diagnostic criteria and fails to confirm the association (p = 0.08 using Dr. Tanzi's favored SDT method and p=0.05 using the S-TDT method; Dr. Tanzi has apparently confused the two methods in his follow-up note of 5/19/99). This indicates the initial result was not robust. The difference is not due to "genotyping differences" - the two datasets were, as Dr. Tanzi knows, "checked side by side" and the results reported to the editor of Nature Genetics. It is not due to differences in the "mode or sensitivity of the genetic analyses performed" - both the genotype and the statistical analyses were performed using the identical methods that were used by Tanzi. It is not due to "much smaller data sets" - both independent datasets had sufficient statistical power to robustly detect the APOE e4 association which Blacker et al suggested has an Odds Ratio equivalent to or less than that of A2M-2.
In his follow-up of 5/19/99, Dr. Tanzi writes: "I would like to point out that Rogaeva et al.'s two sets of independent families are both much smaller than the NIMH set used to find the original association between AD and A2M (Duke: n=65; Toronto: n=40; NIMH: n=400)."
Again, like several other comments made by Dr. Tanzi, this comparison is in fact completely inappropriate. The sample sizes of the Duke and Toronto sub-datasets are correct, and in toto they result in 105 families (which give a non-significant p-value whether they are analyzed together as a single data set or independently as two datasets). However, the stated n-values for the Toronto and Duke subsets are the number of families in each sub-dataset which met the inclusion criteria for SDT analysis described in Dr Tanzi's paper. As such, they are the numbers of families which could ACTUALLY be used in these analyses. In contrast, the "NIMH n = 400" statement is not the sample size of the NIMH data set used for the SDT analysis by Dr Tanzi. Instead, the "NIMH n = 400" is in fact the approximate size of the ENTIRE NIMH sib pair collection, most of which do not fit the structural requirements for the SDT analysis and are therefore unusable. In fact, Dr Tanzi used only 102 NIMH families (compared to 143 NIMH families in our follow up study). The correct statement in the comparison thus should have been that, Dr Tanzi used only 102 NIMH families, and that the size of the combined Duke/Toronto dataset was equivalent to that used by Tanzi et al. and would clearly have the same power to detect an effect as the original Tanzi dataset.
In his follow-up, Dr. Tanzi writes: "Also, as mentioned in our reply in the May, 1999 issue of Nature Genetics, the method used by Rogaeva et al to estimate "power" was basically incorrect since, unlike case-control studies, family-based associations provides [sic] a "conditional" odds ratio. The methods for carrying out these family-based association analyses are for determining "power" in specific sets of families for such analyses are new and unfamiliar to many geneticists."
Again Dr. Tanzi is in error on the facts. We only calculated power for the case-control studies, and we did this using standard approaches. Since we are well aware that calculating power for any family study is a difficult proposition, we simply used as a guide our ability to detect the effect of the APOE-4 allele. In the Blacker et al. paper, the authors state no less than four times that the genetic effect for the A2M-2 allele is similar to, if not greater than, for the APOE-4 allele. Our ability to robustly detect the ApoE4 allele effect (p = 0.0009 even in the smallest sub-dataset) gives practical confidence that the two independent sub-datasets either alone or combined could easily detect associations of a similar.
Dr. Tanzi writes: "To address this possibility [of genotyping differences], over six months ago, we sent our NIMH pedigree and genotype data files to the corresponding author of the Rogaeva et al. study (Lindsay Farrer). However, as of this writing, neither he nor any of his co-authors has replied with any feedback or with any offer to share their raw data, as well."
Thanks for summarizing the three new A2M genetics papers and our reply in Nature Genetics (May 1999) in your "News" section this month. I wanted to share my thoughts on the controversy regarding the candidacy of A2M as a genetic risk factor for AD.
First, I want to clarify a point made in your summary regarding the positive findings in the Rudrasingham et al. paper. These investigators not only confirmed our report of family-based association of A2M and AD in the NIMH families, but they also observed a positive trend in the same direction in an independent albeit smaller set of families (the NIA set). This observation serves as an independent corroboration of our original report of family-based association between A2M and AD. If our original results were spurious (an interpretation favored by Rogaeva et al.), one would not have expected, a priori, to detect a positive trend in this independent set of AD families reported by Rudrasingham et al. While this smaller set of families (with less power) yielded a P=value of .1, the combined p-value for allelic association between AD and A2M in the NIMH and NIA families was statistically quite significant (p=.003) in the Rudrasingham et al study.
These findings thus serve as a confirmation of our original observation of family-based association between A2M and AD. The other study by Rogaeva et al study also demonstrated a significant association of A2M with AD in the NIMH set albeit with a much lower p-value (.05) than that observed in our updated analysis of the NIMH set (.0016; reported in our reply, Nature Genetics, May 1999), and also lower than that reported in the Rudrasingham et al. paper. In two much smaller sets of families (N=45; N=60), Rogaeva et al did not detect a significant association, however, this could be due to power. In addition, this result along with the difference in p-value reported for the NIMH set might be due to the mode and sensitivity of the genetic analyses performed by our respective groups as well as differences in the genotyping.
It may be worth noting that some of the authors on the Rogaeva et al paper recently reported that by genetic linkage analysis using DNA markers, maximum evidence for linkage to AD was found at marker D12S358 which resides very close to A2M (JAMA, 1999). To put this finding in perspective, in the original chromosome 12 linkage paper from Duke (Vance et al., JAMA, 1997), the A2M region of chromosome 12 was NOT tested; the Duke chromosome 12 AD linkage was reported much closer to the centromeric region of chromosome 12. Subsequently, this centromeric localization reported by Duke could not be confirmed by our group (Blacker et al, Nature Genetics 1998) or by two other groups who reported their findings in JAMA (Rogaeva et al, Wu et al., 1998). Both of the latter two papers did, however, report linkage peaks close to A2M. In the Feb., 1999 issue of JAMA, the Duke group went on to extend their analysis of chromosome 12 telomerically toward the A2M region and reported that their most positive linkage peak was also very close to A2M. Thus, traditional genetic linkage findings from numerous groups implicate the telomeric region of the short arm of chromosome 12 directly near A2M (in contrast to the original linkage findings reported by Duke in 1997 which placed the chromosome 12 AD-associated gene much closer to the centromeric region of the chromosome.)
Regarding the discrepant p-values reported by our group and by Rogaeva et al for family based association of A2M and AD, we need to analyze our respective genotypes for the NIMH set side by side to resolve the difference. For example, it is possible that the family material distributed to each site and the exact family members that were genotyped differed or there were differences in the genotypes obtained. To address this possiblity, over six monthes ago, we sent our NIMH pedigree and genotype data files to the corresponding author of the Rogaeva et al. study (Lindsay Farrer). However, as of this writing, niether he nor any of his co-authors has replied with any feedback or with any offer to share their raw data, as well.
Nevertheless, I think the most important point is that two of the three groups who have explored this issue (ours and Rudrasingham et al.)have observed significant family-based association between A2M and AD (while Rogaeva et al report marginally significant findings for the NIMH set). This fact, together with the report of positive case-control studies from Brad Hyman along with the association of an A2M variant with increased amyloid deposition, multiple reports of strong genetic linkage between AD and markers in the A2M region of chromosome 12, and the demonstrated role of A2M in A-beta clearance and degradation suggest that the role of A2M in AD merits further study. Meanwhile, it is has been stated that Haines, Pericak-Vance, Hyslop, Farrer and colleagues will continue to search for another chromosome 12 AD gene. From a historical perspective, it is interesting to note that we and some of the individuals looking at chromosome 12 and A2M chased an AD gene other than APP on chromosome 21 gene for several years at the end of the eighties and into the nineties until Goate et al discovered the APP London mutation. Almost instantly, thereafter, the search for the "other" chromosome 21 gene was abandoned. Genetic analyses from group to group can certainly vary for many different reasons stemming from family and patient material to the types of genetic analyses that are employed. In the end, we all follow our best leads and wherever our data and analyses take us.
Case-control studies in all three Nature Genetic studies were negative. Thus, it is impreative to address the issue of why A2M is associated with AD using family-based association but not population-based analyses. The observation of family-based association of A2M and AD in the absence of any consistently positive population-based (case-control) associations suggests at least one possible explanation. A2M might be operating as a genetic "modifier" for AD, one with significant strength so as to be detected by family-based association but which is missed by most case-control analyses. Basically, we can detect the association of A2M and AD within families where affected and unaffected members share common genetic and to some extent, environmental risk factors. However, in most case-control studies, the association is missed. This may be because the AD cases do not share common genetic backgrounds (opposite to the situation within families). In other words, in the family-based assoication analyses, we may be garnering evidence for a genetic scenario in which certain members of families are getting AD due to various genetic and/or environmental factors, while the A2M variants that have been associated with AD are linked to the rate of pathogenesis (e.g. involving the rate of deposition of A-beta). If A2M were operating as a modifier, its genetic impact on AD would be more easily detected when the affected and unaffected individuals share a common biological background (i.e. common genetic, and to a lesser extent, environmental factors) predisposing to AD. Indeed, A2M has been shown by multiple groups to affect the clearance and degradation of A-beta.
Thus, one possibility is that A2M's role as a genetic modifier for AD is related to the differential ability of common A2M variants to curb the accumulation of beta-amyloid in the brain. Along these lines, my laboratory in collaboration with the company Genoplex in Boulder, CO (for which I am one of three scientific founders) are now focusing on investigating the biological basis for the role of A2M in the clearance and degradation of A-beta for the purposes of drug discovery.
Response from Rudy Tanzi
In Peter Hyslop's reply to the Alzheimer Forum News article on "A2M Revisited, he states: "The Rogaeva et al paper used the SAME family based association statistical methods as Blacker et al (ie the SDT and s-TDT methods). They found NO association in two INDEPENDENT familial AD
datasets, both of which showed prior evidence for linkage with a gene on chromosome 12, and both of which had sufficient power to robustly detect the APOE e4 association using these methods (ie it's not a power problem)."
In reply, I would like to point out that Rogaeva et al's
two sets of indendendent families are both much smaller than the
NIMH set used to find the original association between AD and A2M
(Duke: n=65; Toronto: n=40; NIMH: n=400). Moreover, the ability to
detect family-based association with APOE4 certainly does
not guarantee that one then has the "power" to observe all other
AD-associated genes in these families (e.g. A2M-2) especially given
variable prevalence rates and the heterogeneous biological impact of
different genetic risk factors. If A2M-2 is, as I believe, operating
a genetic modifier, Rogaeva et al could have missed it by testing A2M
in the relatively small Duke and Toronto family sets. Also, as
in our reply in the May, 1999 issue of Nature Genetics, the method
by Rogaeva et al to estimate "power" was basically incorrect since,
unlike case-control studies, family based associations provides a
"conditional" odds ratio. The methods for carrying out these
family-based association analyses and for determining "power" in
specific sets of families for such analyses are new and unfamiliar to
many geneticists. We were very fortunate that in performing these
family-based association analyses of A2M and AD, we had the expert
guidance of Dr. Nan Laird, who developed and published the SDT
Second, given that Rogaeva et al found a p-value of .05 in the NIMH set of families while we get p=.0016 in our extended analyses (see table in our reply; Nature Genetics, May 1999), it is possible that our two teams are not running these analyses (SDT and S-TDT) in exactly the same way as Dr. Hyslop claims in his reply. We also cannot be certain that both teams are genotyping and analyzing the same NIMH samples and/or obtaining the same genotypes for each sibship in this dataset.
We sent Dr. Lindsay Farrer (the corresponding author of the Rogaeva et al paper) our A2M data files several months ago. He could thus confirm our original findings on A2M and AD by running the SDT and S-TDT on our data and then checking whether he finds similar p-values to those we published in our 1998 A2M paper in Nature Genetics. This would also help to determine whether our respective teams are running the family-based association analyses, and particularly the SDT, in the same manner at each site. I also think it would be extremely helpful, if the authors of each of the four A2M/AD studies published in Nature Genetics were to agree, to exchange and cross-analyze each other's published A2M data and then compare the results. Perhaps, by working together in a collegial and constructive manner, we will be able to resolve some of the differences in our respective genetic analyses
of A2M and AD.
The final sentences of the Alzheimer Research Forum News Summary leaves
the impression that the cause of the disparity is due to differences in
the statistical methods used. In fact, this is not at all correct. The
Rogaeva et al paper used the SAME family based association statistical
methods as Blacker et al (ie the SDT and s-TDT methods). They found NO
association in two INDEPENDENT familial AD datasets, both of which
showed prior evidence for linkage with a gene on chromosome 12, and both
of which had sufficient power to robustly detect the APOE e4 association
using these methods (ie it's not a power problem). They also found that
the A2M-2 association degraded to borderline/non-significance when it
was re-tested using the same methods in an enlarged set of families from
the same NIMH dataset originally reported in the Blacker paper.
The Alzheimer Research Forum News Summary omits mention of the
absence of a biological effect of the A2M-2 deletion variant. This is a
rather important element to bring to the attention of non-geneticists
(indeed the editorial from Nature Genetics says that they will now
require future association studies to show a biological effect and
replication in an independent dataset). The Rogaeva et al paper shows
that the A2M-2 variant has no effect on A2M mRNA splicing in brain or
liver; has no effect on monomeric A2M protein size in brain or serum;
and has no effect on A2M protein levels in serum of homozygous or
heterozygous carriers of the A2M-2 deletion variant compared to
homozygous carriers of the insertion variant.