Aging Clocks Catalog · For study teams

Choose a clock for a study

Choose the question first. Then rule out incompatible specimens, targets, populations and implementations.

Foundation reviewed 21 September 2026; reliability and calibration evidence reviewed 22 September 2026; added-information evidence reviewed 27 September 2026. A bounded documentary review, not a diagnostic or treatment service.

A defensible shortlist begins by excluding mismatches. A strong model can be wrong for your study because it predicts the wrong target, requires another specimen or depends on a reference fit you cannot reproduce. The recommendations below are research starting points, not a universal ranking. [M03; M05; SC4; SC6; T01]

Five gates before comparing performance

1. Define the inference and comparator.

   Age resemblance, future outcome prediction and intervention response require different tests. Specify what a clock must add to chronological age, ordinary predictors or direct clinical/functional outcomes.

2. Match the measurement.

   Record specimen, assay generation, feature coverage, the imputer, normalization and reference calibration—not just the platform family. Protein-name overlap is not Olink–SomaScan equivalence; cheek methylation is not automatically whole-blood methylation.

3. Match the population.

   Check age range, sex, ancestry, geography, disease and medication context. External validation in one cohort does not validate every subgroup or use.

4. Match the uncertainty to the task.

   For change, seek absolute within-person error and untreated longitudinal variation—not just calendar-age accuracy or a high reliability coefficient.

5. Freeze an accessible implementation.

   Pin version, coefficients/weights, preprocessing, reference constants, code and permissions before analysis. A model name alone is not a reproducible specification.

These are design safeguards drawn from the methods and feasibility audit, not laboratory practices independently audited on site. [M03; M05; M20; T01; SC3]

Is the new score an addition—or a replacement?

Write down the ordinary base model B, proposed score S, population, outcome and horizon before comparing performance. Evaluate the same eligible people and endpoints where possible, and report who is lost through failed assays or missing clinical inputs. A complete-case comparison alone can conceal the burden of obtaining the extra measurement.

For example, Wang’s UK Biobank Alzheimer’s comparison contrasts brain gap plus demographics with clinical Phenotypic Age, cognition and demographics. It is not an identical-base add-on comparison. The oncology comparison instead keeps a clinical base and tests added MetaboHealth, delta-MetaboAge and hospital albumin. These designs motivate the distinctions above; neither automatically establishes clinical utility. [V05; V01]

External validation of which layer?

1. The assay-to-score model.

   Apply locked features, weights, imputation and reference transformations to a new population.

2. The outcome association.

   Check whether the score retains prognosis there, with the relevant covariates and follow-up.

3. The combined clinical-risk model.

   Externally test a locked B + S against the same B. Refitting the clinical combination and evaluating it locally is a different layer of evidence.

4. The decision.

   Evaluate calibration, usable thresholds and consequences relative to the realistic decision without the added score.

Oh/Wang organ-score transfer supports the first layers; it does not confer external validation on every locally fitted risk combination. Cohorts used earlier for feature selection also are not untouched validation sets: that qualification affects the Deelen and matched GrimAge/MetaboHealth comparisons. A new cohort is not necessarily an independent investigator team. [V04; V05; I02; V03; V02]

Before external validation, identify the computation. Agreement with a library checks implementation parity; it does not by itself establish fidelity to an original method or independent clinical validation. The five computational-evidence distinctions explain why a second arithmetic path or a function’s own output is not an independent reference. [D01; D05; D08]

Write the pipeline beside the clock name

These are proposed reporting requirements grounded in the inspected platform and calibration workflows. For example, missing final predictor probes and a PC model’s larger input set are different coverage problems; “only a few missing probes” is not an error bound. [R04] A separate age calibration can remove a shared offset without establishing absolute agreement.

A concrete trap: two fields in one function family

In the inspected BioAge calculation, phenoage is the generic fitted output; orig=TRUE adds the fixed expression as phenoage0. The returned $fit belongs to the generic model, not the fixed expression. The NHANES helper trains and projects a model without requesting orig=TRUE; a precomputed phenoage0 column is separate. Running the helper with familiar biomarkers therefore does not identify the fixed clock. [D04]

Record the actual path: raw inputs → unit conversions and transforms → fixed constants or fitted reference → output field → any gap/residual mapping. The code-path explanation and existing KDM/HD export leads show what to request. A recipe that exports parameters is not the verified reference payload or an independently established expected output. [D04; D06; D07]

A task-by-model shortlist

Reliability is not a single number

DunedinPACE reports strong same-platform technical-replicate intraclass correlations (ICCs), with lower cross-platform reliability. OMICmAge reports an ICC of 0.998 from 30 replicates. These are useful findings in studied settings—not a commercial service’s universal minimum detectable change. The DunedinPACE reliability datasets differ in design and population, so their ICC differences do not isolate a causal platform penalty. [M05; M21]

Cross-sectional age error is not within-person repeatability. Mean absolute error against calendar age includes calibration, age range and the relation of the training target to birthdays. ICC depends on between-person variance and whether consistency or absolute agreement is being assessed. Neither supplies an individual difference SD by itself. Processing one stored sample twice does not capture collection, shipping or day-to-day physiology. [M05; R03]

PCPhenoAge and PCGrimAge deserve consideration when longitudinal precision matters, but they are different estimators—not silent upgrades to original-clock baselines. Better technical precision does not establish better biological relevance or zero platform bias. [R01]

A concrete version discontinuity: in Tay et al.’s 16 paired same-DNA samples, buffy-coat PCPhenoAge averaged −1.96 score-years for EPICv2 minus EPICv1. Participants were aged 40–60, 14 were Chinese, and the pipeline included EPICv2 imputation. This is combined platform/pipeline evidence, not a universal correction or intervisit error estimate. The worked comparison gives the conditional mean-offset interval. [R05]

Protect the validation from leakage

Keep model development and the claimed validation separate. Feature selection, normalization or residualization using validation outcomes can contaminate the result; any adaptation needs a separately labeled evaluation. Split repeated or family-related data at the participant/family level, single-cell data at least at donor level, and assess device/site effects for imaging. A large test set does not cure a wrong split.

In the brain single-nucleus example, the study includes 73,941 nuclei from 31 postmortem donors. The donor—not each nucleus—is the independent person. Its cell-type resolution does not establish transfer to living-person diagnosis. [M09]

Separate an existing-data analysis from buying a new assay

Report recruitment into the assay subset and reference population, not only total cohort size. The oncology study obtained blood from 39.3% of eligible patients; Wang’s Nurses’ Health Study validation used a female cohort sampled through a nested design. Neither those samples nor a volunteer MRI cohort establish subgroup calibration everywhere. Contemporary delivered assay prices and cost-effectiveness were not verified in this review. [V01; V05; V09]

Keep all model-development stages visible, including earlier feature selection, cohort-specific residualization and risk-model refitting. Fit preprocessing within development data, then evaluate calibration at the intended horizon, discrimination with uncertainty and decision consequences elsewhere. Case–control AUC alone cannot supply population absolute risk; separately centered visits cannot identify a common longitudinal shift. [V03; V07; I02]

A compact record to carry into an analysis plan

Carry the implementation record into the plan alongside validation split, outcome and horizon, ordinary comparator, uncertainty and subgroup checks, rights and runnable artifacts. For an intervention, specify the raw-score/gap/residual/pace contrast, calendar-age handling, assay balancing, missing-data strategy and multiplicity family. For clinical or proteomic retests, missing score-level covariance or repeated predictions remain a reason to withhold an individual threshold—not to borrow methylation-platform variance.

These details matter more than a brand name or “best clock” badge. The benchmark abstract covers 39 biomarkers in more than 20,000 participants and reports little relationship between age accuracy and mortality-prediction capacity. Its full methods were not obtained, so detailed rankings are not adopted. [M06]

Next: Work through intervention endpoints or inspect implementation and access gates.