Specimen Allocation in Longitudinal Biomarker Studies: Controlling Subject-Specific Effects by Design

Addressing issues of quality assurance (QA) when collecting biological specimens and conducting biomarker assays is important to ensure valid and reliable results. While many studies have focused on study designs that collect or analyze one sample per subject (1), less information exists about QA procedures for longitudinal studies in which the primary aim is to examine within-person changes. Because most longitudinal studies have many samples, the samples must be divided into multiple batches for assaying. This batching process can introduce an additional variability beyond the intrinsic, within-batch (intraassay) variation (i.e., batch-to-batch variation; refs. 2-6).

Ideally, batching will not add further variation beyond the intraassay variability; however, it is common for the batch-to-batch variability to be >0 (3, 4). If the samples for a specific participant are assayed in different batches, within-person comparisons could be biased because splitting subjects' samples introduces an additional variation to the within-person comparisons. Designing specimen allocation schemes to minimize the impact of this type of variability is important for obtaining valid and reliable results in longitudinal studies (2-4, 6).

The goal of this article is to better understand specimen allocation factors that may impact biomarker analyses in longitudinal studies that obtain multiple samples per subject. We used data from a randomized clinical trial investigating the effect of a yearlong moderate intensity exercise program versus control on serum levels of endogenous sex hormones in postmenopausal women (7). Among the main outcomes of the study are changes in serum estrone, estradiol, androstenedione, dehydroepiandrosterone (DHEA), and testosterone concentrations. We determined whether assaying samples from the same subject in different batches would influence the association between intervention/control group and changes in hormone concentrations.

The design of the study is described in detail elsewhere (7-9). Briefly, the study investigated the effect of a yearlong moderate intensity exercise intervention in postmenopausal women on serum levels of endogenous sex hormones and, secondarily, changes in weight, body mass index, percentage body fat, and immune function. We randomized 173 postmenopausal women, ages 50 to 75 years, who were sedentary (<20 minutes of exercise three times per week) and overweight (body mass index >25 or between 24.0 and 24.9 kg/m² and a percentage body fat >33%). Participants resided in the Seattle, WA metropolitan area.

The recruitment process identified potentially eligible women primarily via mass mailings and media advertisements (8). Interested women were screened for eligibility by a telephone interview. Major ineligibility criteria included using hormone replacement therapy, being too physically active, and having medical conditions contraindicating moderate-to-vigorous intensity exercise. Eligible women were scheduled for a screening clinic visit to collect baseline data. Those who successfully completed the screening process were randomized to an exercise intervention group (n = 87) or stretching control group (n = 86). Informed consent was obtained following the requirements of the Fred Hutchinson Cancer Research Center Institutional Review Board.

Subjects provided a 50 mL sample of blood after fasting for at least 12 hours, at the screening clinic visit before randomization, and at clinic visits 3 and 12 months postrandomization. Blood was processed within 1 hour of collection; serum, plasma, and buffy coats were aliquoted into 1.8 mL tubes and stored at −70°C in one freezer. Date and time of collection and time since last meal were recorded.

All laboratory assays were performed at the Reproductive Endocrine Research Laboratory (University of Southern California) directed by one of the authors (F.Z. Stanczyk). We include results from the assays (n = 136 subjects) completed between March 2001 and February 2002; assays for the remaining subjects were completed at a later time. Samples were placed into batches such that, within each batch, the number of exercise and control subjects was approximately equal and the sample order was random; subjects were included in approximately chronological order of randomization to minimize bias by differing length of storage time. We created a serum pool from ineligible subjects who had provided a baseline blood sample; the samples used for this pool were from individuals who were postmenopausal and not taking hormone replacement therapy. Two specimens of the pooled sample were placed in each batch; hereafter, these will be called the pooled QA samples. These pooled QA samples were used to determine the assay coefficient of variation (CV). Laboratory personnel were blinded with regard to intervention/control status, which samples belonged to the same subject, and whether the sample was a pooled QA sample.

For 25 subjects (11 intervention and 14 control), the baseline sample was assayed in a different batch from the 3-month and 12-month samples, and in an additional 25 subjects (11 intervention and 14 control), the baseline sample was assayed in a different batch from only the 12-month sample. Data from these subjects are hereafter called the split sample data. Otherwise, all samples from a subject were assayed in the same batch. In February 2002, subjects with samples split into multiple batches were reassayed such that all samples from a subject were assayed in the same batch; these data are hereafter called the reassayed data.

Androstenedione, DHEA, testosterone, estrone, and estradiol were quantified by sensitive and specific RIAs following organic solvent extraction and Celite column partition chromatography (10-13). Chromatographic separation of the five steroids was achieved by use of different concentrations of toluene in isooctane and ethyl acetate in isooctane. Intraassay and interassay CVs were determined using a random effects model to assess the variance components of the results from the pooled QA samples (2, 14) and approximate estimates derived by the delta method (15). The intraassay and interassay CVs were 12.4% and 17.6% for estrone, 12.4% and 15.8% for estradiol, 8.4% and 12.0% for testosterone, 6.1% and 11.6% for DHEA, and 7.4% and 9.8% for androstenedione.

We assessed the effect of assaying the samples of some subjects in different batches on the estimates of the intervention effect on hormone outcomes. To do this, we compared the intervention effect estimate from models including the split sample data versus either excluding that data or using the reassayed data in which all subjects had their samples assayed in the same batch. We modeled the intervention effect at 3 and 12 months separately because a different number of subjects had their samples assayed in different batches at the two time points. Due to the longitudinal nature of the data, we used generalized estimating equations with a Gaussian error, identity link, and an unstructured working correlation matrix (16). We modeled the log-transformed hormone values with indicator variables for batch, month (baseline, 3 months, or 12 months), intervention group, and interactions between month and intervention group as covariates.

The magnitude of the effects of using the split sample data versus either excluding the split sample data or using the reassayed data was quantified by the percentage change in the interaction term regression coefficient, which is an estimate of the intervention effect, between the fits. To compare the model using versus excluding the split sample data, we calculated the difference in the regression coefficient of the interaction term between the two fits and divided by the regression coefficient obtained from the model excluding the split sample data: ∣β_{excluding split sample data} − β_{including split sample data}∣ / β_{excluding split sample data}. The corresponding comparison for the model using the split sample data versus the reassayed data was ∣β_{using reassayed data} − β_{including split sample data}∣ / β_{using reassayed data}. We determined this for both the 3-month and 12-month comparisons.

The regression coefficients of the intervention effect obtained when including the split sample data generally were closer to the null and statistically less significant than those obtained either when excluding the split sample data or using the reassayed data (Table 1). The only exceptions were for the 12-month estradiol intervention effect estimate in which the coefficient moved away from zero when including versus excluding the split sample data and for the 12-month testosterone data in which the effect estimate was nearly zero when using the reassayed data but 0.0171 when using the split sample data. The intervention effect estimate crossed zero in two cases when comparing including versus excluding the split sample data and in two cases when comparing using the split sample versus reassayed data.

The regression coefficients changed appreciably when including the split sample data versus excluding those data or using the reassayed data even after adjusting for batch effects. The percentage difference between the intervention effect coefficients for the models including versus excluding the split sample data ranged from 31.8% for estradiol to 138.3% for testosterone (median 59.6%). Similarly, when using the reassayed data, the percentage difference ranged from 1.7% for androstenedione to 2,237% for testosterone (median 74.6%). The large percentage change for testosterone in both cases was due to the very small intervention effect estimates for that hormone. In general, the percentage differences were larger for the 12-month estimates than for the 3-month estimates. The largest absolute changes occurred for the largest intervention effect estimates.

We were interested in elucidating specimen allocation factors that may impact biomarker analyses in longitudinal studies. The interassay CVs were larger than the intraassay CVs for all the assays, indicating that there is an added variability when using multiple assay batches. This suggests that additional measurement error could be introduced into the effect estimates of longitudinal studies that assess changes of these hormones within subjects. However, this type of measurement error would occur only if the samples from a subject were not assayed in the same batch.

Further, the estimate of the intervention effect changed appreciably when we included the data from subjects whose baseline and follow-up samples were assayed in different batches. Introducing this type of measurement error usually led to a conservative estimate of the intervention effects but sometimes changed the direction of the effect, although, in the latter situation, the effect estimates from one of the models was very close to the null. This is consistent with the literature, which suggests that measurement error in outcome measures of longitudinal studies can lead to bias (17, 18).

These data indicate that sample allocation is an extremely important design issue in longitudinal studies. Cohort or intervention studies primarily interested in assessing changes in biomarkers over time should assay the baseline and follow-up samples together; baseline samples should not be assayed alone to assess baseline cross-sectional associations more quickly. This concept may also be extended to other study designs. For example, in matched case-control studies, a case and its matched control or controls should be assayed in the same batch. A problem with batching may also occur in case-cohort designs in which a random sample of the cohort is assayed at one point and all cases are assayed at a later time. Bias may be introduced due to interassay variability or a systematic change in the overall mean levels, strengthening arguments to use nested case-control studies.

The subjects whose samples were assayed in different batches were chosen from the first 136 women randomized so that the assays could begin before the end of the trial. Slightly more control (n = 28) than intervention women (n = 22) had split samples, although the difference was not statistically significant. In addition, each comparison model (excluding the split sample data or using the reassayed data) has some limitations. Specifically, the model that excludes the split sample data has a different subset of subjects than the model including that data; this could partly explain the difference in the estimates rather than measurement error. Further, the model using the reassayed data has slightly different covariates than the model using the split sample data because of the additional indicator variables needed for the reassay batches. In this case, differences in the estimates could be partly due to the different covariate adjustment. However, despite these possible limitations, we noted a similar pattern of measurement error introduced by assaying the baseline and follow-up samples from a subject in different batches with both comparison models.

In conclusion, longitudinal studies using biomarker outcomes must be carefully designed to avoid unnecessary measurement error and variability. It is useful to include blinded replicates of a single, and preferably pooled, sample in each batch to determine the intraassay and interassay CVs. This information can be useful when interpreting the results of a trial, particularly if the expected changes are small or the effect estimates are not significant. In addition, all samples from an individual subject or matched set of subjects should be assayed in the same batch to reduce measurement error when estimating changes in outcomes over time and to better assure unbiased estimates.