Young-Geier Autism Study: What the—? (Part 2)

The following is the second installment of a review of "Thimerosal exposure in infants and neurodevelopmental disorders," by Young et al, which links thimerosal exposure to autism. Statements from the materials and methods section are discussed, with otherwise heavy deferrals to EpiWonk.

The study protocol employed was approved by the US [CDC], the Institutional Review Board (IRB) of Kaiser North-West, and the IRB of Kaiser Northern California. The data were analyzed at the secure Research Data Center of the National Center for Health Statistics in Hyattsville, MD.

Alleged violations of this study's protocol by the Geiers (father-and-son duo) are discussed here and here. According to an 05/21/08 e-mail from the Kaiser IRB office, the objections stated in 2004 by the CDC and Kaiser were resolved, and the study was ultimately approved by the IRB. However, Kaiser did not specify how the objections were resolved. At the time of this post, a statement from the CDC regarding the alleged protocol violations is pending.

The study was conducted based upon a retrospective ecological [emphasis added] assessment of neurodevelopment disorders that were identified a priori as possibly related to Hg exposure.

There are several uses of the term "ecological" in the article to describe this study and others. Perhaps EpiWonk can provide some insight into the word's meaning in this context; the distinction's lost on me. The authors acknowledge the preselection of a list of neurodevelopmental disorders (eg, autism) that are presumptively (ie, "a priori") related to mercury exposure.

Only those individuals who had a non-missing date of birth and were born before January 1, 1997 were examined. This date was chosen to allow for at least 4 years of follow-up for each member of the cohort which was believed to be an adequate amount of time to observe the outcomes of interest.

Here the authors acknowledge that a minimum 4-year time frame should be sufficient to assess the occurrence of preselected neurodevelopmental disorders in the VSD, which was created in 1991 and updated through the year 2000. However, the authors later contend that the time frame is not sufficient, to justify their addition of presumptive cases. (An aside: Data from Kaiser North-West, Kaiser Northern California, and Kaiser Colorado were examined by Young et al; however, an IRB nod from Kaiser Colorado was not mentioned in the previous, relevant paragraph.) 

All children who received an oral polio vaccine within 3 months of their birth date and who were born before January 1, 1997 were used as the denominator or population at risk for this study.

The time period for the study is from 1990 (0.6% of the study population) to 1996, inclusive. A total of 278,624 children were identified. (Another aside: Because of the very rare incidence of vaccine-induced polio associated with the administration of the oral vaccine [1 case in 2.4 million doses], it was recommended in 2000 that all US children should receive only inactivated polio vaccine).

The outcome files (inpatient and outpatient diagnoses) from this population were then reviewed to find the first instance of diagnosis of the disorders of interest. If there were multiple instances of the same diagnosis in a child, only the first instance of diagnosis was counted. Then the total numbers of each diagnosis for each disorder of interest were determined by birth cohort. The counts of each diagnosis of interest represented the numerator or outcomes for this study.

Okay, I'm still following along at this point. The authors tallied the first instance of each preselected ICD-9 code and divvied the total counts by birth cohort (ie, year). Referral to Table 2 reveals, for instance, that there were 583 identified cases of autistic disorder, current or residual (ICD-9 codes 299.00, 299.01), among the 278,624 children (ages 4-10 years) who received oral polio vaccine within 3 months of birth, to produce an overall 0.21% frequency of autistic disorder. However, note in Table 2 that the authors' adjusted overall prevalence rate for autism is 25.4/10,000, or 0.254%. More on this later.

The prevalence of each diagnosis was then calculated by birth cohort by dividing the count of a diagnosis in that birth year by the total number of children from the study population that were born in that same year.

The number of children per birth cohort (year) can be calculated by using percentage data in Table 1; however, the raw numbers of autism (and other) cases by birth year are not provided. (Figure 1 does provide graphically the number of autism cases per 10,000 per year [with imputed data for 1995 and 1996 presumably included—as indicated, more on added cases later]). EpiWonk talks extensively about birth year as a confounder in this study.

Because of concern that the cohorts from 1995-1996 had only 4-6 years of follow-up, frequency distributions of age at diagnosis were examined for all years. This revealed that for some of the disorders a sizable proportion of children were diagnosed after 4.5 years. Adjustments were made for counts of cases as needed for birth cohorts depending upon the disorders examined to correct for under ascertainment that occurred due to shorter follow-up times. These adjustments were made for all disorders including the control disorders as appropriate based on the age distribution.

Although the authors originally proposed that 4 years of follow-up would be sufficient, they now conclude that more follow-up time is needed. This conclusion is presumably based on their discovery in earlier birth cohorts that, for some of the ICD-9 codes (essentially all of the neurodevelopmental conditions, except 315.9), the median (not mean) age at diagnosis was 4.5 years or older (Table 2). Therefore, the authors made "adjustments" to "correct for under ascertainment" by adding cases "as appropriate." EpiWonk talks about this "extremely dubious" imputation of data here. Also, although the authors say that "adjustments were made for all disorders including the control disorders," Table 2 reveals that the median ages for these conditions (pneumonia, congenital anomalies, failure to thrive) were below the 4-year time frame, suggesting that "adjustments" may not have been necessary for these particular control conditions.

For example, 37% of autism cases in the study were diagnosed after 5 years old with about 50% diagnosed after 4.5 years old. This is a conservative estimate since it includes the 2 years (1995-1996) that had shorter follow-up times. Examination of the distribution of age of diagnosis by birth year for autism revealed that only about 15% of cases were diagnosed after 5 years of age in the 1995 birth cohort while the 1996 cohort had no cases diagnosed after 5 years of age and only 3.5% of cases diagnosed between 4.5 and 5 years of age.

So among the 583 total number of autism cases identified in the VSD (which presumably do not include the imputed cases), a little more than 200 (~37%) were diagnosed after 5 years of age. The authors argue that this is an underestimate because of the relatively shorter follow-up times for the 1995 and 1996 cohorts. For the 1995 cohorts (with presumably 6 years of follow-up, 1995-2000 inclusive), 15% of cases (not 37%) were diagnosed after 5 years of age. Because the follow-up for the 1996 cohort was 1 year less, no cases of autism were detected after 5 years of age.

Based on the average age at diagnosis for all cohorts, the 1995 count of autism cases was increased by 45 cases with the assumption that all of these would have been added in the 5 year+ age group (bringing this percentage close to the overall average of 37% diagnosed after 5 years of age). The same was done for 1996, but the number of cases was augmented by 80 because it was assumed that these would be diagnosed in the 4.5 to 5 and 5+ groups essentially bringing the percentage diagnosed after age 4.5 close to the overall average of 50% diagnosed after 4.5 years of age. The new augmented frequency counts of cases in 1995 and 1996 birth cohorts were then used as the new case counts in the analysis. 

Here's where my head starts to rotate on its axis. The number of autism cases for the 1995 cohort were increased by 45 to increase the rate of autism cases diagnosed after the age of 5 years from 15% to 37%. Therefore, we can conclude that 22% (37% – 15%) of the imputed autism cases for 1995 equals 45 cases. Working backwards, we can actually estimate raw data from the later birth cohorts. There were approximately 160 autism cases orginally identified in the 1995 cohort (45/22 x 100 = 205; 205 – 45 = 160). Therefore, the original rate of autism for the 1995 cohort (using data from Table 1) was 0.31%; the imputed rate is 0.39%. Similar calculations can be performed for the 1996 cohort. Eighty cases of autism were originally identified in the 1996 cohort, for a rate of 0.17%; the imputed rate is double that, or 0.33%. (Also note that the authors now refer to the "average age at diagnosis," not the median age. It's unclear if the lack of the distinction between median and average age is an oversight or an intentional slide.)

For the entire "autism" cohort (all birth years), 125 cases were added. By using data from Table 2, we can calculate how many cases were added overall for each diagnosis, with the presumption that most (if not all) cases were added to the birth cohort data for 1995 and 1996.

Condition	n	Prevalence Rate, %	Adjusted Prevalence Rate, %	Calculated No. Added Cases
Neurodevelopmental
Autism	583	0.209	0.254	125
Autism spectrum	817	0.293	0.367	206
Hyperkinetic syndrome	5712	2.05	2.51	1281
Developmental disorder/ learning disorder—not otherwise specified	2248	0.807	0.948	393
Disturbance of emotions	1694	0.608	0.762	429
Tics	804	0.289	0.389	280
Control
Pneumonia	33,648	12.1	13.2	3130
Congenital anomalies	1643	0.59	6.32	15,966
Failure to thrive	4754	1.71	1.85	401

For the neurodevelopmental disorders, the number of cases overall were typically increased by approximately 20%-25%, with the exception of tic cases, which were increased by approximately 35%. The control cases (excepting congenital anomalies) were increased by much less, approximately 10%. (It is assumed that the adjusted prevalence rate for congenital anomalies [63.2/1000] is almost certainly a typo and should be 63.2/10,000. It is also assumed that ~1597 cases were added to the database, not 15,966 as calculated by the numbers given.)

In analyzing the adjustments made for follow-up corrections, varying levels of imputing additional cases were modeled to assess the sensitivity of the results to the assumptions made when imputing additional cases in specific birth cohorts. Sensitivity analyses revealed that point estimates were similar even when imputing 50% fewer cases than would be expected using the average age distributions as noted above. In addition, confidence intervals showed little variation and maintained statistical significance when imputing as low as 25% fewer cases than would be expected using the average age distributions.

Head now spinning like Michael Keaton's in Beetlejuice. How I read the above: the authors extensively monkeyed with the outcome data to determine how much "imputation" the data (or we) could possibly stand.

Because the study protocol did not permit us to match data across vaccine files, exposure was determined in aggregate by birth cohort for each vaccine and then summed across birth cohorts. The routine childhood vaccines of interest were Haemophilus influenza type b (Hib), hepatitis B vaccine, [DTaP], and [DTP] vaccines.

Young et al assumed that the mercury content from Thimerosal provided by each vaccine dose would be 25 µg, with the exception of hepatitis B vaccine (12.5 µg per dose). The authors cite the FDA study by Ball et al from 1999, which indicates that Thimerosal-free vaccines were available for Hib (FDA approved September and November 1996), DTaP (January 1997), and a combination Hib-hepatitis B vaccine (October 1996). So it is possible that children in the VSD, specifically those in the later birth cohorts, may have received some Thimerosal-free vaccines (Hib at 2, 4-6, and ≥12 months; DTaP at 2, 4, 6, and 15-18 months; and the combination Hib-hepatitis B at times of Hib administration). Nevertheless, Young et al assumed the mercury content per vaccine dose as described.

Within each vaccine file, the cumulative Hg dose for each individual was calculated based on the number of each type of vaccine received...This calculation resulted in an average Hg dose per person for each birth cohort which served as the exposure variable. Because of interest in particular windows of exposure, Hg doses from vaccine exposure were calculated for the following periods: 1) birth to 7 months; and 2) birth to 13 months. 

In other words, the authors tallied up the number of Hib, hepatitis B, DTaP, and DTP vaccines received from birth to 7 months or birth to 13 months for each birth-year cohort. So for every dose of Hib, DTaP, or DTP vaccine dose, 25 µg of mercury was added; for every hepatitis B vaccine dose, 12.5 µg was added. Young et al then divided that cumulative mercury dose for each birth-year cohort by the number of children in the cohort—for instance, approximately 51,267 for 1995. This number, the average mercury dose per person per birth cohort, was designated the "exposure variable."

Logic would dictate that the cited cases in the VSD could have received no vaccines (other than oral polio) between birth and 7 months or a maximum of 3 Hib, 3 DTaP, and 4 hepatitis B vaccines (including one at birth) during that time frame, for an ethylmercury dose ranging from 0 to 200 µg. Figure 1 bears out this thinking, with the exposure variable ranging from ~110 µg (for 1990) to ~145 µg (for 1992). 

Graphs plotting the Hg dose by birth cohort as well as prevalence of a particular disorder by birth cohort were constructed. Poisson regression analysis was used to model the association between prevalence of event of interest and Hg dose...Parameter estimates from Poisson regression models were used to obtain rate ratios. Hg dose was modeled as a continuous variable and rate ratio estimates and 95% confidence intervals were calculated to determine the change in prevalence rate of each diagnosis per unit increase in Hg dose from Thimerosal-containing vaccines.

So after all the aforementioned maneuvers, Young et al estimated a rate (or risk) ratio for each diagnosis per each 100-µg change in mercury exposure by using Poisson regression models, which is about as useful to me as saying, "Presto Change-o." It's now a deep-field punt to EpiWonk to discuss (further) the use and validity of a Poisson regression to estimate these ratios; but before I do, I ask 2 questions in particular: 1) Is it appropriate to assume a linear regression between ethylmercury and the ICD-9 codes, especially when considering such miniscule doses of ethylmercury? 2) Given that the average ethylmercury exposure per birth cohort is somewhere between 100 and 150 µg, does it make sense to stratify disease risk on the basis of 100-µg changes in ethylmercury exposure?

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Conclusions: The most concerning methodologic issue in the study by Young et al is the liberal imputation of cases, which the authors justify on the basis of shorter follow-up times for later birth-year cohorts. The practice challenges credulity, in part because the percentage increases for neurodevelopmental diagnoses are so much higher than those for control cases (discounting congenital anomaly data). But also, the authors do not provide enough raw data (eg, prevalence rates per birth cohort) to enable the confirmation of data. The authors also make assumptions about the amount of ethylmercury delivered from vaccines, particularly in later years, which may not be accurate. Some Thimerosal-free vaccines were available in late 1996 and may have been administered to children in the 1995 or 1996 birth cohorts.

Last, the estimated rate ratios per change in mercury exposure demand a considerable amount of trust from the (nonstatistician) reader, which is sharply limited in this writer after the authors' imputation of cases.

Next: Results.