Rapamycin: the mouse lifespan effect is real. What is missing in humans?

Substantive correction, 20 September 2026: We rechecked the original papers, supplements and calculations. This revision corrects removals counted as pretreatment deaths, entry ages and a sex label. It withdraws claims of saturation at the lowest dose, equivalence of cyclic and continuous treatment, exclusion of effects through retrospective power, and commercial-equivalent milligram doses inferred from a 24-hour blood concentration. PEARL analysis denominators, inconsistencies in its tables, RAPA-EX results, figures and the reproducibility package have been updated.

01Repeated mouse survival effects, rather than one fixed percentage

The ITP studies four-way-cross UM-HET3 mice at TJL, UM and UT. We used 17 available cohort files from C2004–C2021, without claiming that they cover the entire current archive. The 36,975 source rows included three identical removal records for one non-rapamycin C2020 mouse. After removing two redundant rows, there are 36,973 unique animal identifiers, 35,297 death endpoints and 1,676 removals. Death includes protocol-defined terminal euthanasia. Rapamycin monotherapy accounts for eight arms and 2,388 mice, with three additional combination arms. ITP archive

Parts per million means milligrams per kilogram of feed, not an individual animal's intake or blood concentration. Harrison 2009, Miller 2011, Miller 2014, Strong 2020

The main analysis compares animals still under observation at treatment entry, against controls of the same cohort and sex, using site-stratified Cox models. This conditions on surviving and remaining in the study until entry; it does not remove earlier chow differences. Multiple arms within a cohort share controls and are not independent replications. Treatment was assigned by cage, but usable cage identifiers are absent from these lifespan files. Our intervals and tests are therefore at the animal level, without a cage correlation adjustment.

For continuous 14 ppm treatment, male hazard ratios in three cohorts are approximately 0.59, 0.59 and 0.72; female estimates are 0.45, 0.38 and 0.30. These support benefits in the same direction across separate batches. They do not establish a constant effect: starting ages differ, and a heterogeneity test with only three cohorts cannot establish equivalence.

On an absolute scale, the C2009 42 ppm arm adds 105 days of restricted mean survival in males (95% interval 53–157) and 202 days in females (169–236), from approximately day 270 through age 1200 days. These are differences in areas under survival curves within a common observation window, not extra human years or identical gains for every mouse. Some comparisons violate proportional hazards, so a hazard ratio is a model-dependent follow-up summary. The calculation tables also provide results through age 1095 days.

02Separate deaths from removals before dosing

Before day 600 in C2005, the male rapamycin arm had 22 deaths and seven removals; controls had 90 deaths and 19 removals. The previous article added both categories and called them deaths, while actually using a cutoff of approximately 609 days.

After separating events and censoring, Kaplan–Meier estimates of pretreatment mortality are approximately 12.8% and 24.7%. The site-stratified log-rank P is 0.0012, or 0.019 after Holm adjustment across 16 monotherapy arm-by-sex comparisons. A difference before dosing cannot be caused by rapamycin. The original paper identifies early chow source or formulation differences at UT and UM; TJL did not have that chow difference. Harrison 2009

The C2015 paper also describes different pretreatment food suppliers and separation of survival curves. With corrected death/removal coding, the male continuous-treatment pretreatment comparison gives P=0.059, or 0.83 across the 16-test family. The previous claim of significant pretreatment mortality imbalance in both late-start cohorts should not stand. Conversely, a nonsignificant P does not demonstrate exchangeable groups. Strong 2020

The paper-table audit uncovered another estimand mismatch: Miller 2011's average 10% increase in male median lifespan is the average of three site-specific percentage changes, not the median change after pooling all mice. The current archive gives a death-only median of 813 days for UT male controls; the paper prints 780. Rounding cannot explain that difference. The low-dose C2009 UM male median increase is approximately 7%, which also does not reproduce the printed 16%. Other cells agree, but these discrepancies remain unresolved. A similar P value cannot establish correct input interpretation. Harrison 2009 additionally used an earlier analysis cutoff than the complete archive. We retain the cell-by-cell comparisons and describe our estimates as a reanalysis of the available current archive, withdrawing the claim of exact reproduction for 16 of 17 targets. Miller 2011, Miller 2014

03Dose and schedule require direct comparisons

The three C2009 doses share controls and can be compared in one categorical-dose model. In females, the hazard ratio for 14 versus 4.7 ppm is 0.62 (0.47–0.80), and for 42 versus 4.7 ppm it is 0.58 (0.45–0.75). Both retain statistical support after Holm adjustment across six pairwise comparisons per sex. Saturation at the lowest dose is not supported.

A difference between 42 and 14 ppm is less clear: the female hazard ratio is 0.94 (0.73–1.23), and the male estimate is 0.85 (0.66–1.09). These intervals do not establish equivalence. A categorical dose-by-sex interaction supports sex-dependent effects, but three nonzero doses cannot determine an optimal dose or a complete saturation curve. The former test of departure from log(ppm+1) tests a chosen functional form, not biological monotonicity.

This four-arm model uses different risk sets from the separate two-arm models in the previous figure, so its estimates differ slightly. Both stratify by site; their numbers should not be interchanged.

C2015 compares three schedules at 42 ppm within one cohort. In females, stopping after three months versus continuing gives a hazard ratio of 1.81 (1.40–2.33), with a difference surviving multiplicity adjustment. Short exposure cannot be equated with continued treatment. Cyclic versus continuous treatment gives 1.29 (approximately 1.00–1.66), an unadjusted P around 0.051 and a six-comparison adjusted P around 0.10. This is neither equivalence evidence nor proof of no difference.

The original paper's analysis of all assigned animals reports a survival benefit from three-month treatment in males; our analysis conditional on being observed at day 604 does not reach the conventional significance threshold. Estimands, risk sets and methods differ, and both deserve explanation rather than selection according to a preferred schedule. The original paper also reports weaker effects of cyclic than continuous exposure in females; our conditional contrast and its uncertainty are given above. Similarly, a nine- versus twenty-month comparison across cohorts is not a randomized early-versus-late trial. Strong 2020

04Removals matter, and cross-experiment rankings have limits

In C2009 males, removal rises from 1.7% in controls to 23.1% at 42 ppm. The paper describes removal of entire cages after fighting injuries, and discusses both behaviour and wound healing as possible explanations. Some published percentages use cages as the denominator; ours use animals and cannot be directly matched. Females do not show the same dose gradient. Miller 2014

Different removal proportions do not automatically prove informative censoring. The concern is whether the unobserved survival of removed animals differs from that of animals remaining in the study. We examined an adverse-to-treatment scenario: treated removals die at removal, while removed controls survive to the longest observation time. The male 42 ppm hazard ratio changes from 0.59 (0.48–0.74) to 0.79 (0.64–0.97). Its direction persists in this scenario, but these are specified replacement rules, not universal mathematical worst-case bounds. They do not resolve cage correlation or problems in other cohorts.

Across the 17 files, 93 male and 89 female treatment-versus-own-control comparisons are estimable. Female rapamycin and combination-arm point estimates cluster toward the stronger protective end; other compounds also have strong male estimates. Cohorts, starting ages, doses, schedules and control lifespans differ, and shared controls correlate estimates. The distribution below provides archive context, not comparative drug efficacy or a ranking of human prospects. ITP archive, Combination cohort, Rapamycin and acarbose

05PEARL neither demonstrates longer life nor proves no effect through power

PEARL was a 48-week randomized placebo-controlled trial using nominal weekly doses of 5 or 10 mg of compounded rapamycin. These are study conditions, not recommended regimens. Its primary measure was DXA visceral adiposity, alongside lean tissue, bone measures, blood markers and self-report questionnaires. PEARL

The published flow diagram lists 125 randomized participants and the text reports 114 completers. Completion does not mean complete measurements: the 48-week visceral-fat analysis contains 89 people; female lean tissue analysis contains 33, comprising seven higher-dose, 11 placebo and 15 lower-dose participants. The current registry separately lists actual enrollment of 129, an unexplained discrepancy that we cannot fill by inventing four participants' outcomes. Supplements, Registry

The abstract's visceral-fat P=0.942 corresponds to a supplementary repeated-measures mixed ANOVA, F(2,85)=0.060. The three-group comparison at 48 weeks instead gives F(2,86)=0.335 and P=0.716. Neither clearly detects a difference, but they are different tests.

Actual contrast intervals are more informative about precision. At 48 weeks, the higher-dose versus placebo difference in visceral-fat percentage change from each individual's baseline is approximately −7.23 percentage points, with the original within-analysis, three-comparison-adjusted 95% interval from −34.78 to 20.31. The interval accommodates effects in either direction. Substituting 114 participants into a different one-way ANOVA power calculation cannot establish that moderate or larger effects have been excluded. Equivalence also requires a specified margin assessed against an actual interval.

Female lean tissue does show a signal worth following: the higher-dose versus placebo difference in percentage change is approximately +6.19 points, with the original three-comparison-adjusted interval of 0.88–11.51. This is a between-group difference in relative change, not a 6.19 kg gain. The printed F(2,30)=5.052 implies partial eta squared of approximately 0.252. The body of the paper labels 0.202 as epsilon squared; its abstract uses a different symbol. Our previous article then treated these as interchangeable in a power argument.

We reproduced contrasts from the published means, standard deviations and counts, and added sensitivity analyses allowing unequal variances. For the higher dose at 48 weeks, the female-minus-male treatment-effect difference is approximately 5.04 percentage points, with an exploratory 95% interval of −1.20 to 11.28. Significance in women and nonsignificance in men do not establish a sex difference. None of the four dose-by-time sex contrasts passes a Holm adjustment. This also does not demonstrate equal responses.

The main paper separately prints 24 body-composition odds ratios. Treating that table as one sensitivity family leaves no result below 0.05 with Holm or BH adjustment; the smallest adjusted P is 0.192. This is not a complete trial-wide correction and does not show that every signal is false. Continuous outcomes and odds of improvement require separate interpretation.

Two reporting issues also matter: the improvement definitions, timing and interval methods for some printed odds ratios are insufficiently specified, and supplementary bone-density summaries include −100% changes and unusually large dispersion without explaining the underlying coding. Without individual records, we cannot determine whether these reflect missing-data handling, measurement or reporting errors; an interval lacking log symmetry alone does not establish an error. We therefore do not treat the lower-dose bone-density OR of 0.24 as confirmed bone loss. SF-36 and WOMAC are absent from the current registered endpoint list and are presented as exploratory observations in the paper; positive results require independent confirmation.

06A concentration difference is not an equivalent dose

The formulation comparison comes from a separate nonrandomized study: 23 of 67 users took compounded rapamycin and 44 took commercial products, with different doses and prescribing choices. Approximately 24 hours after dosing, mean dose-normalized concentrations were about 0.27 versus 0.87 ng/mL/mg, a ratio near 31%. Another observational cohort was examined, and the authors also reported differences in assayed product content. Formulation study

This supports concern that the same nominal milligrams can produce different exposure and that formulation needs checking. A single time point across nonrandomized groups cannot determine AUC, peak concentration, tissue exposure or mTOR inhibition. PEARL's 5 and 10 mg cannot be multiplied by one third and labelled 1.7 and 3.3 mg commercial-equivalent doses. Nor does this comparison establish insufficient dosing as the explanation for PEARL's negative result.

Mechanistically, the rapamycin–FKBP12 complex allosterically inhibits mTORC1. It is not an ATP-competitive inhibitor; substrate responses differ, and prolonged exposure can affect mTORC2 in some cells. Several causal steps remain between pathway inhibition, improvement in one measure and longer healthy survival. Feldman 2009, Pharmacology review

07New human functional evidence and safety questions

Human functional trials already exist. RAPA-EX, published in 2026, randomized 40 adults aged 65–85, with both groups undertaking 13 weeks of home exercise. Adding weekly sirolimus did not demonstrate additional chair-stand benefit: the primary intention-to-treat difference was −2.13 repetitions (95% interval −4.61 to 0.34). Complete-case and per-protocol results more strongly favoured placebo, but their populations and assumptions differ and they cannot replace the primary result. This raises a possibility of impaired short-term exercise adaptation, not a conclusion of harm for every person and schedule. RAPA-EX trial

PEARL's main text reports 122, 116 and 117 nonserious adverse events in placebo, lower-dose and higher-dose groups, respectively, and 3, 2 and 1 serious events. Its supplement, however, reclassifies one placebo event as nonserious and explicitly includes a placebo participant who died without completing the trial. The detailed higher-dose AE table has 36 rows, also differing from the 35 completers. Event counts, people with events, completer counts and observed exposure time are not interchangeable. The previous estimate of 114×48 weeks, or approximately 105 participant-years of exposure, was not supported by actual dosing and follow-up records and has been withdrawn. PEARL supplements

RAPA-EX reports at least one AE in 17 of 20 people in each arm, with one serious pneumonia considered possibly drug related. Its reported 99 versus 63 event counts depend on counting rules. The row-level audit in our protein article found that the authors' filtering excluded events lacking end dates and longer events; we therefore do not treat that count ratio as a fully established incidence rate. Laboratory group means within reference ranges also cannot exclude individual abnormalities or long-term risk. RAPA-EX, Related analysis

The official sirolimus label identifies risks including infection, oral mucosal problems, lipid changes and impaired wound healing. Approved populations, concomitant drugs and exposure differ from healthy-adult trials. Transplant risk rates cannot simply be transferred, and similar short-term event counts in small trials cannot establish long-term safety. Official label

Mouse functional evidence is mixed as well. Wilkinson and colleagues found improvements in several age-related tissue and activity measures, alongside increased testicular degeneration and cataracts. In a different male mouse strain, Neff and colleagues found that some apparent improvements also occurred in young animals, suggesting age-independent drug effects. Strain, endpoints, starting ages and control designs differ; merely calling the papers contradictory is insufficient. Lifespan records alone contain none of these functional or pathology measurements and cannot adjudicate a universal slowing of aging. Wilkinson 2012, Neff 2013

Immune trials of rapalogs or other mTOR-related drugs provide related evidence, not substitutes for rapamycin efficacy. The phase III RTB101 respiratory-illness trial did not meet its primary endpoint. This illustrates the need for direct clinical testing, rather than showing that every mTOR intervention has failed. Mannick 2021

08What this study supports

The evidence supports survival benefits in multiple UM-HET3 cohorts and substantial dependence on dose, sex and schedule. It does not establish human lifespan or disease-free survival benefits, an optimal dose or schedule, uniform functional improvement, or long-term safety.

We retain data versions, original-table discrepancies, code, complete comparisons and negative results. This analysis plan was revised in response to identified errors after the earlier results were known; it is a public correction, not a new preregistration. Mouse Cox and restricted mean survival estimates were checked with independent implementations. Human calculations use published summaries, without claiming access to PEARL individual data. Download the reproducibility package.

More discriminating evidence would come from randomized trials with characterized exposure, complete follow-up and attrition records, prespecified functional or disease endpoints, and joint assessment of benefits and harms. Models and biomarkers can help formulate hypotheses; they cannot answer in place of those outcomes.