Choosing Controls From Biobanks and Population Cohorts

Why Control Selection Matters

In a rare-variant sequencing study, controls help estimate how often variants occur in the population from which the cases arose. A large biobank can make control recruitment convenient, but its participants are not automatically suitable controls. A person without a diagnosis in the available records may have an undetected condition, may be too young to have passed through the relevant risk period, or may not have been eligible to become a case under the study’s definition.

The central design question is therefore not simply whether controls are currently labeled “unaffected.” It is whether they represent the relevant noncase group for the cases, target population, and disease endpoint being studied. Poor control selection can distort the estimated genetic contrast even when the case sample is correctly defined and the sequencing analysis is carried out as planned.

Definition: A control is a study participant selected to represent the noncase or at-risk comparison group specified by the study design. The source population is the population that gave rise to the cases and to which the study’s comparison is intended to apply. Control eligibility must be defined with respect to the same target population, disease definition, and relevant time point used for the cases.

For a conventional case-control comparison at a fixed endpoint, controls should meet the study’s eligibility criteria and have no evidence of the defined disease by that endpoint. Other designs can use a different rule. For example, in risk-set sampling, a person who later becomes a case may serve as a control at an earlier event time, when that person was still at risk. The design must state which interpretation applies; “control” is not a universal synonym for “will never develop the disease.”

Assessing Biobank and Cohort Controls

Biobanks and population cohorts can provide controls efficiently, with existing participant information and stored samples. Their main design advantage is scale; their main challenge is determining whether recorded data establish the control status the analysis requires. A defensible assessment addresses phenotype verification, age and follow-up, and eligibility before counting participants as controls.

Design question	What to establish	Potential consequence if overlooked
Phenotype verification	How disease absence was determined, and how complete the relevant records are	Cases may be incorrectly included among controls
Age and follow-up	Whether participants have reached the relevant risk period and have enough observation to assess the endpoint	Participants who will later become cases may be treated as confirmed noncases
Eligibility	Whether controls satisfy the same population and study-entry criteria relevant to the cases	The comparison may concern different underlying populations
Control reuse	Whether the same controls contribute to more than one case comparison or analysis	Analyses may be dependent even when the case groups differ

Phenotype evidence can range from detailed clinical review to diagnostic codes, self-report, or the absence of a diagnosis in available records. These sources do not provide equal assurance. A code-based screen may miss disease when care occurred outside the linked system; self-report can be incomplete; and no recorded diagnosis is not proof of no disease. A study should describe its evidence for control status and, where feasible, validate it against clinical records or other relevant data.

Age and follow-up matter whenever the disease can arise after enrollment. A participant who is disease-free at age 45 is not necessarily a valid control for a disease defined by onset before age 70. Likewise, follow-up that ends before the relevant endpoint leaves future status unresolved. The appropriate classification depends on the study’s estimand: a fixed age-specific endpoint requires evidence through that endpoint, while a design that samples people at risk at particular event times has its own risk-set definition.

Eligibility should be checked in the same substantive terms for cases and controls. If cases come from a defined geographic catchment and satisfy particular age and clinical criteria, controls should be drawn from the population that could have contributed eligible cases. This does not require controls to be identical to cases in every observed characteristic. It requires the comparison group to be appropriate for the intended contrast, with any remaining design or analysis choices stated clearly.

Worked Example: Verifying Controls for an Age-Specific Endpoint

Suppose a hypothetical study defines its outcome as diagnosis of a disease by age 70 among adults in a specified catchment area. A cohort contains 1,200 otherwise eligible participants. Of these, 500 have reached age 70 and have records covering the period through age 70; 15 were diagnosed by that age. The other 700 are currently aged 50 to 69 and have no recorded diagnosis so far.

Apply the endpoint definition. For this fixed age-70 endpoint, the 500 participants with complete observation through age 70 can be classified with respect to the required time point. Of these, \(500-15=485\) have no diagnosis by age 70 and are potential controls, subject to the remaining eligibility checks.

Do not count unresolved status as confirmed absence. The 700 younger participants have not yet reached age 70. Their lack of a recorded diagnosis today does not establish that they remained disease-free through the study’s endpoint. They should not be counted as confirmed controls for this particular endpoint on the information given.

The example does not mean that younger participants can never contribute to a genetic study. They could be used under a design that explicitly handles age and incomplete follow-up. The conclusion here is narrower: for the stated fixed endpoint, the evidence supports 485 potential controls, not 1,185.

How Incorrect Controls Change the Contrast

If people with the disease are mistakenly included among fixed-endpoint controls, the control group becomes a mixture of true noncases and cases. The following calculation gives a simple description of the resulting change in an allele-frequency contrast. It assumes that the control sample is a random mixture, that a fraction \(r\) are actually cases, and that allele frequencies in the two groups are \(q_0\) for true noncases and \(q_1\) for cases. It is an illustration of phenotype contamination, not a general correction for every sequencing design.

q_{\mathrm{control,obs}}=(1-r)q_0+rq_1

The observed difference between case and control allele frequencies is then

q_1-q_{\mathrm{control,obs}} =q_1-\{(1-r)q_0+rq_1\} =(1-r)(q_1-q_0).

Thus, under these assumptions, contamination moves the control frequency toward the case frequency and reduces the observed contrast by the factor \(1-r\). This arithmetic explains why even a modest fraction of misclassified controls can matter. It does not imply that every effect estimate or gene-level test is attenuated by precisely this factor: that depends on the outcome, sampling, variant aggregation, and analysis.

Worked Example: Quantifying Phenotype Contamination

Consider a hypothetical sequencing study in which the allele frequency is \(q_1=0.012\) among cases and \(q_0=0.004\) among true noncases. Suppose 10% of the proposed controls are actually cases because disease status was incompletely verified. Here \(r=0.10\).

Calculate the observed control frequency.

q_{\mathrm{control,obs}} =(1-0.10)(0.004)+(0.10)(0.012) =0.0036+0.0012 =0.0048.

Compare the contrasts. With correctly classified controls, the case-control difference is \(0.012-0.004=0.008\), or 0.8 percentage points. With the contaminated controls, it is \(0.012-0.0048=0.0072\), or 0.72 percentage points. Equivalently, \(0.90(0.008)=0.0072\), as the mixture derivation predicts.

Under the stated mixture assumptions, the control contamination reduces this allele-frequency difference by 10%. The calculation does not identify the actual contamination rate in a real biobank; that requires evidence about phenotype ascertainment.

Reusing Shared Controls

A control group may be used for more than one case group, for example when two studies or two disease subgroups share a common comparison sample. Reuse can be efficient, but it does not turn one set of controls into multiple independent sets. Any analyses using the same estimated control frequency share sampling uncertainty and are therefore statistically dependent.

To see the issue, let \(\hat{p}_{C1}\) and \(\hat{p}_{C2}\) be carrier proportions in two independent case groups, and let \(\hat{p}_0\) be the carrier proportion in one shared control group. The two estimated contrasts are \(D_1=\hat{p}_{C1}-\hat{p}_0\) and \(D_2=\hat{p}_{C2}-\hat{p}_0\). If the case samples are independent of one another and of the controls, their covariance is

\operatorname{Cov}(D_1,D_2) =\operatorname{Cov}(\hat{p}_{C1}-\hat{p}_0,\hat{p}_{C2}-\hat{p}_0) =\operatorname{Var}(\hat{p}_0).

The shared control term appears in both contrasts, so its sampling variation links them. A joint analysis or a synthesis of the results should account for this dependence. Counting the same controls twice as if they were distinct participants can understate uncertainty and overstate the amount of independent information.

Worked Example: Two Comparisons With One Control Group

Suppose two hypothetical, independent case groups are each compared with the same 600 controls. Among the controls, 12 carry a variant, so the estimated control carrier proportion is \(\hat{p}_0=12/600=0.0200\). For a sample proportion, the estimated variance under independent Bernoulli sampling is \(\hat{p}_0(1-\hat{p}_0)/n\).

\widehat{\operatorname{Var}}(\hat{p}_0) =\frac{0.0200(1-0.0200)}{600} =\frac{0.0196}{600} \approx 0.00003267.

Because both contrasts subtract this same \(\hat{p}_0\), their estimated covariance from the shared controls is approximately \(0.00003267\). The corresponding estimated correlation cannot be calculated from the control data alone; it also depends on the variances of the two case proportions. The key design conclusion is already clear: there are 600 control participants, not 1,200 independent control participants. Any analysis combining the two comparisons must retain the shared-control dependence.

A Practical Evaluation Sequence

A control source should be assessed before sequencing results are interpreted. The following sequence makes the design decisions explicit and separates phenotype evidence from sample size.

Specify the endpoint.
State the disease definition and the time point or risk-set rule that determines who is a case and who is eligible as a control.

Define the source population.
Describe who could have contributed eligible cases, including relevant study-entry criteria, and identify how the candidate controls relate to that population.

Audit control status.
Record how absence of disease was established, what records were available, and whether age and follow-up cover the required endpoint.

Track overlap.
Document whether controls are shared across comparisons so the analysis does not treat overlapping samples as independent.

A useful report distinguishes the number screened from the number whose status is adequately established. It should also describe the rules for excluding ineligible participants and the evidence supporting those rules. These details let readers judge whether a large control sample is also a relevant control sample.

Common Mistakes and Why the Choice Matters

“No diagnosis in the biobank means unaffected.” This treats missing or incomplete records as clinical evidence. Instead, describe the ascertainment method and assess whether it can establish disease absence for the intended endpoint.
“Younger participants are controls because they are healthy now.” Current status does not establish status through a later age-specific endpoint. Use a design and analysis appropriate for incomplete follow-up, or restrict the fixed-endpoint control definition to participants with adequate observation.
“A very large cohort automatically gives a better control group.” Size cannot repair a mismatch in eligibility or phenotype definition. First establish relevance; then assess how much usable information the eligible controls provide.
“The same controls count separately in every comparison.” Reuse may increase efficiency, but it does not create new independent observations. Preserve the overlap in the variance calculation or joint analysis.

Key takeaway: Choose controls by a stated disease endpoint, source population, and eligibility rule. Verify that age, follow-up, and phenotype evidence support the required control status, and account for dependence whenever controls are reused.

Check Your Understanding

Use the study endpoint and sampling design to justify each answer.

Why is absence of a diagnosis code not necessarily evidence that a biobank participant is disease-free?
A study defines disease by age 65. What information is needed before a 50-year-old participant with no recorded diagnosis can be classified as a control for a fixed age-65 endpoint?
In the mixture model, what happens to the case-control allele-frequency difference as the fraction \(r\) of misclassified controls increases?
Why can a control who later becomes a case still be eligible in a risk-set sampling design?
Two case groups use the same controls. Explain why their estimated contrasts are not independent, even if the case groups are disjoint.