Rebuttal to Ajioka and Kushner

It is, indeed, important to ensure that the results are not due to such bias, and this is a consideration that we addressed carefully and from several points of view in our studies. Nonetheless, it appears to be an aspect of our study frequently singled out by those who found it difficult to reconcile our results with their own notions of the penetrance. The authors of one of the letters cited by Drs Ajioka and Kushner averred that our patients were “sickly”;1 another letter2 suggested that the subject population was too healthy. Both criticisms cannot be correct. But selection biases can occur, and we have examined the data using 2 independent methods to determine whether such a bias existed.

As pointed out in “The Cys282Tyr mutation as a necessary but not sufficient cause of clinical hereditary hemochromatosis,” the first of these methods examines the distribution of genotypes among white subjects according to the Hardy-Weinberg equilibrium. If there were a hereditary disease in which half the homozygotes were healthy and the other half died, a population such as the one we studied could lead to the erroneous conclusion that the disease had no phenotype, since those who had perished would not attend a health appraisal clinic. Conversely, if we were studying a disease such as hereditary hemochromatosis from the vantage point of a liver clinic, as was done, for example, by Niederau and Strohmeyer,3 we might accumulate an excess of homozygous patients with cirrhosis. But if there were no selection for or against homozygotes the distribution should follow the expression p2 + 2pq + q2, where p is the gene frequency of the wild-type allele and q that of the mutant (Cys282Tyr) allele. If our selection of patients excluded the 10% or 20% of very ill patients that some suggest exist, a deficit of homozygotes (q2) would exist. In fact, there is actually a slight surplus, although not a statistically significant one. The surplus is even more prominent (expected of 93 vs observed of 107) if we limit our population to those 19 733 patients who reported only northern and western European ancestry (Table1).

Analysis of the age distribution of the patients revealed no significant lack of older subjects with the homozygous genotype. Poulos et al4 suggest that “…they took no account of demographic changes in southern California in the past few decades. Immigration of younger Hispanic and Asian populations, in which there is a lower prevalence of Cys282Tyr homozygosity, would have a confounding effect by diluting the prevalence in younger age groups.” In point of fact, we were keenly aware of the possible confounding effect of ethnic origin on age distributions and all of our age distribution studies were confined to white non-Hispanic subjects. This point was unfortunately not clear in our original The Lancet publication, but it has been clarified since.5,6 We are not the only investigators to find that homozygotes are equally represented among old populations. Ajioka and Kushner dismiss Willis et al's observation of no decrease in prevalence of homozygosity for Cys282Tyr among the old because only death was considered as a criterion, but cite the only study7 in which a slight deficit of homozygotes and heterozygotes was claimed in which death is also the only criterion. The results reported by Bathum et al7 in homozygotes was not statistically significant; all other recent studies confirm that there is no deficit of homozygotes among the very old,8,9and increased longevity among Cys282Tyr carriers has even been claimed.10 Yet, unless there is a counterbalancing effect that increases survival there should be a very small decrease of the number of aged subjects who are homozygous since we know that the severe disease can be lethal. It is simply that even very large studies such as ours cannot discern the effect because it is so small. Indeed, a very recent extension and re-evaluation of our data shows a small difference in homozygous males, but this difference is not statistically significant.6 

Drs Ajioka and Kushner suggest that “unbiased” studies support their view of a higher penetrance of the homozygous state. Surprisingly, they allege that the Norwegian study by Asberg et al11 demonstrates a penetrance of 10% with respect to fibrosis or cirrhosis. We calculate a penetrance for severe cirrhosis of 1.0% from the same data. The 10% figure seems to have been derived by using the number of subjects biopsied as a denominator rather than the total number of homozygotes in the population. This is a very small subset of all of the homozygotes, consisting only of those who had the highest ferritin values and whose doctors apparently considered biopsy desirable, clearly a group very strongly biased toward patients with severe disease. Obviously an estimate of penetrance not subject to selection bias must be based upon all homozygotes in the population studied. Since genotypes were determined only on persons with high transferrin saturations, the gene frequency must be calculated from the Norwegian population. Fortunately such data exist and predict that there would be approximately 400 homozygotes in the group of 65 238 subjects examined. Only 4 patients (1.0%) were found to have cirrhosis, as we pointed out in our commentary, hardly a strong argument for high penetrance. If penetrance is extended to include fibrosis, the number increases to 12, a frequency of 3.0%. The percentages of these changes in males would be nearly doubled, since almost all of the liver abnormalities were found in male subjects.

In another study, the percentage of biopsies of 215 cirrhotic livers and hepatomas that were found to have the Cys282Tyr/Cys282Tyr genotype were compared with the frequency in the general population. The best estimate of the occurrence of cirrhosis or liver cancer in the lifetime of a homozygote was 2.7%.12 

While we are confident that our study has not been compromised by ascertainment bias, we are concerned that studies that suggest that the penetrance of the disease is very high are affected by another type of bias, namely, observer bias. They are also compromised by the lack of suitable controls. Observer bias is a serious consideration in any scientific investigation, and especially so when subjective judgments such as the presence of symptoms, such as fatigue or symptoms of arthritis, are at issue. It is not a question of honesty, but rather that the judgments the observer makes are inevitably unconsciously influenced by knowledge of many factors other than the piece of datum being evaluated. Such bias clearly extends to radiologic and morphologic assessments. The radiologic manifestations of hemochromatosis arthropathy are not so unambiguous and distinctive that all will agree about an interpretation, and we have found no blinded studies that provide unbiased data on the specificity and sensitivity of joint examination with respect to a diagnosis of hemochromatosis. Excellent pathologists will disagree about the extent of fibrosis or whether it is present at all. It is for this reason that a blinded evaluation is needed; both the examiner and the patient must be unaware of the genotype, and this was carefully built into our experimental design. The hemochromatosis and iron overload screening (HEIRS) study, to which Ajioka and Kushner refer, does not have such a feature. It may therefore provide useful data about gene frequencies and biochemical phenotypes, but will not be able to provide robust information about many important clinical aspects of the disease. Moreover, it is not clear that the HEIRS study population is free of ascertainment bias. This study is to be carried out on patients recruited from health maintenance organizations, a diagnostic blood collection center, public and private primary care offices, and walk-in clinics.13 Thus, it would seem that the population consists primarily of those seeking health care, and a strong selection bias in the direction of people with clinical problems would seem to exist.

In the past few months since my commentary was written other assessments of the hemochromatosis phenotype have been made by 2 independent groups in different countries. Both of their results agree with ours. Very recently more data were reported from the Norwegian study, data concerning clinical manifestations in patients who had not been informed of their diagnosis; observer error had been minimized or eliminated. This, too, is a group that Drs Ajioka and Kushner accept as being free of selection bias. Asberg et al14 write, “Compared to control persons, phenotypic and genotypic HH men and women had a higher score on 1 of 17 questions dealing with joint complaints. Women below 50 years of age had a higher prevalence of hypothyroidism (15.2% and 12.5%, respectively, compared to 3.0% in the control population). Phenotypic HH women below 50 years of age had higher diastolic blood pressure than control women. Phenotypic HH men above 50 years of age and genotypic HH men scored lower than control men on a compound myocardial infarction risk score variable, in part due to lower serum cholesterol concentration. Fewer phenotypic HH men above 50 years of age reported having angina pectoris. Otherwise, the health of phenotypic and genotypic HH persons was not different from the health of control persons” (emphasis added). It is worth pointing out that many of the differences that were noted are probably not related to hemochromatosis but represent the invariable result of multiple comparisons in a large study.

Figure1shows the results of the patients' assessment of their general health in the Norwegian study. It is clear, first of all, that there is no difference between homozygotes and controls with respect to the percentage who do not enjoy excellent or good health. In both groups, the percentage is lower than in the population studied at Kaiser, and this may well be due to the older age of the Kaiser population and, importantly, in the way the question was posed. At Kaiser we used an extensively validated questionnaire that had been used for some 12 years; it may be that the wording of the question, that is, “My health limits activity to some degree” was too sensitive in picking up minor dysfunction, particularly in older people.

Another, quite different study of an unbiased population of more than 1 000 000 has just been published. This paper, published under the declarative title, “Hereditary haemochromatosis: only 1% of adult HFE C282Y homozygotes in South Wales have a clinical diagnosis of iron overload”15 is based on the actual diagnosis of iron-storage disease in the community. The authors conclude, “A systematic review of all possible records of patients diagnosed and treated for HH over a 2-year period within 2 health districts in Wales has revealed that only 1.2% (n = 76) of Cys282Tyr homozygotes have been diagnosed as having iron overload and received treatment. Once diagnosed, the degree of iron-loading was often modest.”

There are 2 possible sources of error in such a study. Some of the patients diagnosed apparently had very little storage iron. Did they really have clinical hemochromatosis? On the other hand, were all patients with the disease properly diagnosed? The authors of the study consider this source of error and deem it to be unlikely.

Drs Ajioka and Kushner are puzzled that in an earlier publication, based on the same Kaiser population, my collaborator, Dr Felitti, averred that the penetrance of hemochromatosis was very high; most of the patients had clinical stigmata of the disease. The population of patients has not changed materially, and if selection bias had been the cause of the low penetrance we observed Dr Felitti should have observed such low penetrance as well. The difference was not due to selection bias, but rather to observer bias. When Dr Felitti and I began our fruitful collaboration in studying the Kaiser population both of us believed that the penetrance of hemochromatosis was quite high. That is what everyone believed. But being keenly aware of potential observer bias we designed our study in such a way that this type of bias could not affect the outcome. When we published our results for the first time in abstract form,16 Dr Felitti was so taken aback by how different the outcome appeared to be from what had been our preconceived idea that he declined to have his name listed as a coauthor until he had had the opportunity to personally review the data. It was only after he had satisfied himself that the penetrance was as low as we had calculated it to be that he allowed himself to be listed as a coauthor. It reminded him, he told me, of a double-blind study of the effect of amantadine on influenza infection in which he had been involved in the 1960s. There was one patient who stood out in everyone's mind as an example of how dramatic the effect of this drug could be on the symptoms of the disease. When the study was unblinded, this patient, to everyone's surprise, proved to be one who had been in the placebo control group.

Although I consider it very likely that observer bias has played a role in increasing the apparent penetrance of the homozygous state in some study, the fact is that there is very little difference between the data reported by groups claiming high penetrance and those who consider penetrance to be low. The difference is largely a philosophic one. What is penetrance? Ajioka and Kushner consider any homozygote who has hepatic fibrosisor increased liver-function tests orradiologic evidence of hemochromatotic arthropathy to have “disease-related morbidity.” We, on the other hand, have limited our definition of penetrance to the development of ill health or shortening of life span. I consider these as the clinically relevant end points, but if we had selected pathologic end points our assessment of penetrance would have given results quite close to those who maintain that penetrance is high. Our studies do agree with Ajioka and Kushner's contention and the studies of Olynyk et al17that hepatic abnormalities occur in a modest proportion of persons with the Cys282Tyr homozygous genotype. Unfortunately we were unable, for ethical reasons, to offer liver biopsies to our patients. Thus, our study suffers from the necessity to depend upon surrogate markers. Among the homozygotes 8.2% manifested increased aminotransferase activity (AST) levels, compared with only 3.2% of matched controls. Serum collagen IV levels, considered a good surrogate for hepatic fibrosis, were elevated in 25.8% of the homozygotes compared with only 11.1% of matched controls. In the small series reported by Olynk et al17 4 of 16 subjects were found to have fibrosis, a figure very close to the one provided by our surrogate marker. Had we considered anyone with either an elevated AST or elevated collagen as manifesting “disease-related morbidity” our estimate of penetrance would be 39 of 152 or 26% (if not corrected for wild-type controls) just on hepatic abnormalities. This is very close to the percentage of patients that Ajioka and Kushner have designated as manifesting “disease-related morbidity.”

Ajioka and Kushner have chosen pathologic manifestations as their standard of penetrance because they make the reasonable assumption that patients with fibrosis and cirrhosis are likely to become ill. But this is unproved, and the data from our study and other large population studies suggest that it is probably not correct. Liver-function tests were not significantly more abnormal in older patients or in those with very high ferritin levels. Moreover, if 10% or 20% of patients with hemochromatosis became seriously ill, where are they? They did not disappear from the Kaiser population, since the homozygotes were all accounted for. They were not found in the Welsh study.15 They did not appear in a study of autopsy and biopsy tissue by Willis et al.12 As noted above, all but one study show that homozygotes are not underrepresented at old ages. The disagreement is not so much in the data but in the interpretation of what changes in liver function, liver histology, or bone x-rays mean to the quality and length of life of homozygotes.

The main justification for determining the penetrance of the Cys282Tyr homozygous state is that it might help us in medical decision making. I am frequently asked about 2 issues: (1) Should we phlebotomize homozygotes, particularly those with elevated ferritin levels? and (2) Should we screen? The answer to the first question is quite simple. We might as well. It will not harm the patient; it may prevent the very rare progression of disease that we know may occur but that we cannot yet predict, and if the blood is, as it should be, used for transfusion purposes, some good will come of it. Moreover, given the activities of support groups and the beliefs of some physicians, patients will be difficult to convince that phlebotomy is not needed. Even if they are convinced not to be phlebotomized they may be certain that any disease they develop later in life was the consequence of untreated hemochromatosis, and the physician will surely hear of it. The second question is one of public policy. It raises complex issues of balancing cost and possible psychologic and physical harm to the patient against years of life saved. The cost must be balanced against other public health measures such as nutrition and prevention of infectious disease. Interestingly, Asberg et al,18whose data show extremely low penetrance, suggest that screening, nonetheless, is cost effective. In my view the flood of data that is becoming available will soon make it clear to everyone how low the penetrance of hemochromatosis is. The debate about screening will, I am sure, continue.

This is manuscript number 15074-MEM.