Aging Clocks Catalog · How claims are assessed

How the evidence is judged

Reliable measurement, prediction, intervention response and better health decisions are different achievements. No single statistic establishes them all.

Foundation reviewed 21 September 2026; reliability and calibration evidence reviewed 22 September 2026; intervention evidence reviewed 26 September 2026. A bounded documentary review, not a diagnostic or treatment service.

The important question is not whether a clock is “validated” in the abstract. It is validated for which claim, in which setting, with which implementation? Consistent measurement, external prognosis, treatment response, clinical utility and surrogate validity are distinct. A research biomarker can be useful without meeting the last two standards. [M03; M05; M26]

A claim needs the right kind of evidence

Assessment standards informed by the inspected methods, controlled studies and FDA–NIH BEST definitions; not a claim that every paper was designed to satisfy every row. [M03; M05; M11; M20; M25; M26; SC1]

Five different meanings of “the calculation checks out”

Computational-identity evidence reviewed 29 September 2026 strengthens the source and software checks behind the clinical example. It does not supply an independently established primary-method expected output or clinical validation. Keep these five claims separate when accepting a tool or interpreting a report.

The exact unmet gate: a complete permitted input with its units/transforms, source and reference revision, expected output and precision, plus a provenance chain independent of the implementation being accepted. Original-author certification would be strong evidence, but a separately established primary-method reference computation can also qualify. A lone score, molecular coefficient list, shared spreadsheet derivation or self-generated test expectation is insufficient. This bounded search did not show that such evidence is absent everywhere. [D01; D08]

The named formula comparisons and existing KDM/HD export designs are useful progress. Neither an export recipe nor source-level parity closes the independent-output gate. Static explanations remain supported; a preset feature still needs separate reference, source-choice and rights review.

A software discrepancy is not automatically a published-study error. Establishing that stronger claim would require the study’s actual revision, preprocessing, reference and execution chain. The conflicting 2019 equation was read from publisher-extracted PDF text but could not be visually verified after rendering failed; the 2018 equations were visually checked. The maintainer’s attributed author confirmation is not independently authenticated correspondence. Those limits narrow the claim without erasing the documented code history. [D01; D02; D03]

Three separate questions before interpreting a change

1. Does it exceed the relevant error?

   First match the output and complete pipeline. Identical numerical inputs test software reproducibility; a split specimen tests only steps after the split; separate collections include collection and intervening physiology. Paired version bridges estimate platform/pipeline disagreement. State bias and absolute difference variance for the relevant experiment rather than substitute calendar-age error or an ICC. [R03; R05]

2. Does it reflect the intended biological construct?

   A real inflammatory or cell-mixture change is not automatically sustained aging. Examine standardized repeated visits, untreated trajectories and independent functional or clinical measures. The inspected timing study’s dense series was one person and its additional paired data came from a stress experiment; it supports attention to context, not a universal daily age fluctuation. [R08; R09; R11]

3. Does using it improve a decision?

   Identify the action triggered by the score and compare benefits, harms and costs with a realistic no-test decision. Even a resolved, biologically relevant change does not establish clinical utility. Surrogacy separately requires treatment effects on the marker to predict clinical effects in a defined context. [M26]

No single reliability coefficient answers all three. Under a stable, approximately normal, unbiased error process, 1.96 × SD(error difference) is a statistical repeatability bound—not a clinically important difference. In general, Var(e₂ − e₁) = Var(e₂) + Var(e₁) − 2 Cov(e₁, e₂); the equal-independent-error shortcut is a special case. This is a measurement model, not an estimated threshold for any product. The matched-platform example estimates a mean version offset, not same-platform intervisit variation.

A group contrast is not an individual response classifier

For a hypothetical balanced trial with independent participants, n per arm and individual-change measurement-error SD sD, the measurement-error component of the difference-in-mean-changes has standard error sD × √(2/n). This excludes biological heterogeneity, clustering, missingness and systematic batch bias. More participants can reduce random error in a group contrast; they do not remove an arm-confounded shift. A statistically detectable group effect can therefore be smaller than an individual repeatability bound without contradiction.

The CALERIE control back-conversion illustrates why output definition also matters: its PCGrimAge summary is a group age-gap change standardized by baseline dispersion, not individual measurement error or raw-age change. [R09]

Noise does not always make an effect a lower bound. Under additive, mean-zero outcome error independent of treatment, an unstandardized randomized contrast has unchanged expectation and greater variance. Standardized effects may shrink when noise inflates the scale SD; systematic or treatment-dependent error can behave differently. This is reasoning under a specified measurement model, not an estimate of CALERIE’s error process or evidence of “at least this much” aging improvement. [S08]

The missing uncertainty for clinical and proteomic scores

Repeating a deterministic formula on identical values cannot estimate the covariance below. The source and parity checks establish computational properties; collection, assay and intervisit error require measurements under the relevant protocol.

Clinical-laboratory composites: for a fixed linear score, input-error contribution is w′Σw: weights combined with the covariance matrix of input errors in the correct transformed units. The inspected clinical Phenotypic Age formula is linear in those transformed inputs, including log CRP, when calendar age is treated as known. A serial-use interval additionally requires collection/physiological and cross-visit covariance for the proposed timing. Those matrices were not established for the inspected services. Adding or averaging analyte CVs cannot recover them. [M03; R15]

Proteomic clocks: a linear score likewise needs weighted covariance; for a nonlinear clock, full-pipeline replicated predictions under the actual specimen, panel, preprocessing and model version are the more direct empirical check. Average protein ICCs or a count of reproducible proteins do not supply final-score error. A small preanalytical experiment found altered inflammatory-protein measurements despite analytical controls, but calculated no aging clock; it cannot establish error in ProtAge, PAC or rentosertib’s six outputs. [R10; R11]

Clinical-laboratory and proteomic individual-change thresholds therefore remain unresolved for the specific services and pipelines inspected. Neither methylation-platform variance nor external risk association fills the missing score-level evidence.

Numbers only mean something with their comparator

Mean absolute error for calendar age does not measure longitudinal reliability or outcome prediction. A hazard ratio describes conditional association under a fitted model. A C-statistic measures ranking; it does not establish that a predicted 10% risk occurs 10% of the time. That last question concerns calibration. Clinical utility additionally asks what happens when a decision changes because of the result.

The NMR example reports five-year C-statistics of 0.837 versus 0.772, and ten-year values of 0.830 versus 0.790, in FINRISK. It has a real conventional-risk comparison, but cohort-based scaling limits immediate individual classification and the models were not simply the same base with one extra predictor. The worked application preserves that boundary. [M11]

CALERIE: what a rounded p-value can and cannot settle

The favorable DunedinPACE group response remains beside the PCPhenoAge and PCGrimAge null contrasts. The catalog’s sensitivity audit transcribed 40 published summaries: 22 intention-to-treat (ITT) tests from Table S4, six primary-model treatment-on-treated tests, and 12 cell-adjusted ITT/TOT tests from S6. These are comparison rows, not people or independent replications. [S08]

Two declared sensitivity families: six ITT comparisons (three primary models × two visits), and all 22 S4 ITT comparisons (11 implementations × two visits). Bonferroni and Holm were applied at familywise alpha 0.05. These are the catalog’s sensitivity choices—not the paper’s original p < 0.005 convention, proof of a prespecified family, or coverage of every exploratory, subgroup and mediation test. Both corrections can address dependent tests; neither repairs invalid input p-values, selection or model misspecification.

*Assuming nearest rounding to the last displayed digit, printed 24-month p = 0.002 has the conservative envelope [0.0015, 0.0025]. The 12-month p = 4.83E-04 retains its displayed precision, half-width 0.0000005. The envelopes propagate printed precision through the corrections; they are not confidence intervals. A different printing rule would require a different envelope. Published pointwise effect intervals were not adjusted. [S08]

These results do not negate the group response or identify the best clock. The other S4 ITT models do not become significant through these corrections. Participant-level mixed models, instrumental-variable estimates, mediation and methylation predictions were not refitted. Correlated outcomes and two visits are not independent clinical replications. The application also retains the less favorable cell-adjusted TOT result, rather than claiming unchanged robustness under every sensitivity. [S08]

Mediation is not the same as clinical-surrogate validation

CALERIE did analyze mediation. Its models connected DunedinPACE change with changes in clinical and blood-chemistry outcomes. Figure S4 describes small mediated fractions. Many intervals for the proportion mediated excluded zero; intervals for the average causal mediation effect (ACME) included zero except for log CRP and clinical Phenotypic Age. The latter is the clinical-laboratory composite, not PC DNAmPhenoAge. No precise indirect effects were digitized or re-estimated by the catalog. [S08]

Causal mediation additionally needs assumptions about mediator–outcome confounding, treatment-induced confounders, model specification and measurement. The inspected code uses pace change and outcome change over the same baseline-to-24-month interval; it does not establish temporal precedence. A risk-marker mediation model in one trial does not establish fewer deaths, longer life or trial-level clinical surrogacy. [S08; S09; S11]

A marker need not itself cause benefit to be predictively useful. Conversely, evidence for one causal pathway does not establish the net clinical effects of every treatment that moves the marker. Statistical mediation is neither a universal prerequisite nor sufficient evidence for every surrogate use. A relevant validation should include independent interventions and discordant outcomes, not only favorable examples. [S10; S11]

The rentosertib distinction: a low clock–FVC R-squared is not mediation and does not isolate an independent aging mechanism. The reported 100,000 patient-label randomizations are meaningful evidence against the specified exchangeable-label null, but do not randomize mechanisms, undo selection or validate a clinical surrogate. Benjamini–Hochberg is not automatically invalid because clocks correlate; its guarantees depend on the dependence conditions and valid input p-values. Actual numerical rows and the complete permutation implementation remain unverified. [SC1; S05; S10]

What a favorable summary must not hide

What this review did

This is a purposive, claim-driven documentary review with foundation evidence/access observations dated 21 September 2026, a reliability/calibration follow-up dated 22 September 2026, and intervention evidence dated 26 September 2026. It follows selected original methods and validations; separates parent and ancillary trials; inspects public product/legal documents; and reads code where it changes feasibility. It is not a systematic review, market census, pooled meta-analysis or product certification. Search visibility was not treated as popularity or market share.

“Inspected” means the stated relevant text was read—not every citation, figure or supplement. Some emerging-family entries and the 2025 benchmark rely only on abstracts/metadata. The foundation used publisher-provided ProtAge and CALERIE text delivered on ResearchGate; unrelated citing-paper snippets were excluded. The follow-up also inspected CALERIE’s university-hosted publisher supplement and Tay’s Supplementary Table S4 visually. Source access depth remains specific to each entry, not an assertion that all supplements were read.

All study numbers are author-reported unless explicitly identified as arithmetic. No participant-level dataset was obtained, clock package run, restricted model acquired, product purchased or seller contacted. The follow-up reconstructed agreement limits for all 18 selected specimen/model rows in Tay’s rounded S4 aggregates, keeping age and pace units separate, and checked consistency with reported rounding. It added conditional normal-theory intervals, back-converted rounded CALERIE group summaries and checked fixed synthetic clinical/calibration examples. It did not reproduce raw-pair nonparametric tests, methylation processing, imputation or clock fitting. [R05; R09; R15]

The intervention follow-up inspected official registry mirrors, the public parent protocol and embedded statistical section, a reporting form, peer-review exchanges, CALERIE numerical supplements and author code. It recovered cohort/arm flow and executed multiplicity/rounding sensitivities on 40 published summaries. It did not rerun rentosertib S2–S5 tests or patient-label randomizations, or CALERIE mixed, instrumental-variable or mediation models. Documentary verification, aggregate arithmetic and recomputing molecular predictions remain three different levels of work. [S03; S04; S05; S06; S07; S08; S09]

The computational-identity follow-up, observed on 29 September 2026, inspected primary equations, revision history, helper/output paths, tests and existing export designs. It executed one byte-pinned Biolearn function in isolation and checked declared mathematics on three inherited synthetic cases. No whole clock package, reference fit, export notebook or empirical workflow was run. The independent expected-output gate remains open. [D01; D03; D05; D08]

How to read the local source labels

M identifies scientific methods/validation or the official terminology framework; SC identifies the six-clock case, parent trial and model/access sources; C identifies seller/contract documents; T identifies implementation documentation; R labels identify the reliability/calibration evidence review; S labels identify the intervention follow-up. Existing SC1/SC2 notes record their deeper follow-up inspection. They are source identifiers, not quality scores. A local source note tells you the inspected depth and relevant conflicts. A source’s availability does not give another source’s claims its authority.

Original papers support scientific claims; sellers describe their own offerings and terms; current code documentation describes access, not what an older trial necessarily ran. A “latest” documentation address is mutable. The date attached to the review is not a new publication date, a purchase guarantee or a claim that every underlying experiment was recent.

The paired-platform reconstruction assumes independent participants and approximately normal, homogeneous differences within each specimen/model. Rounded aggregates cannot test those assumptions, outliers, proportional bias or subgroup behavior. The intervals are pointwise rather than simultaneous over all rows. S4 and main-text SDs disagree in some rows, and a normalization name/reference inconsistency remains; S4 was used without inventing unrounded data or silently resolving preprocessing. [R05]

What would materially strengthen the conclusions?

For an individual retest: independent, matched collection-to-report repeatability, untreated longitudinal variation, exact report-version correspondence and a demonstrated decision advantage. An unrelated age-error statistic would not resolve the gap.

For the IPF case: a reconciled registry and protocol-revision history, the final approved analysis plan and laboratory/plate records, actual numerical S2–S5 rows, trial-specific artifacts and change-score covariance. The public protocol and ancillary arm counts are no longer missing. Reproducing statistical tests from predictions would still not equal recomputing those predictions from raw proteins.

For CALERIE: unrounded p-values for the expanded-family 24-month boundary and a source-pinned reproduction of the relevant models, including mediation. Neither its group intervals nor statistical mediation supplies individual-change uncertainty or clinical-surrogate validation.

For clinical risk use: external calibration and threshold/net-benefit evaluation against a realistic current comparator, followed by evidence on the decisions and outcomes produced by using the score. One more adjusted association would not by itself settle utility.

Next: Inspect the three worked evidence chains or separate public code from reproducible access.