Every claim, and what it does not support.
The register
Every rule Fermata enforces must trace to an entry here. Each records what its source supports and what it does not support.
13 entries, 12 verified against the primary source. The register is small on purpose: it covers only what Fermata actually claims.
E1Verified Tendon stiffness does not change significantly before ~12 weeks of strength training, while muscle strength rises ~40% and neural activation ~9% in the same window (knee extensors, patellar/Achilles tendons).
- Supports
- Progression gates must not open on strength performance alone. A trainee's capability outruns their connective tissue by roughly a month — the window where "I felt ready" and "I got hurt" coincide. Minimum dwell time in a loading phase is a defensible rule.
- Does not support
- Any specific per-day loading prescription. Any claim about wrist or shoulder tendon specifically — this studied knee extensors and the patellar/Achilles tendons only. Any claim that respecting the lag prevents injury; it establishes a timeline, not an intervention.
E2Verified Chronic wrist pain is reported by 56.7% of adult handstand practitioners (n=321 survey), against a 4-6% general-population rate.
- Supports
- Treating wrist load as a first-class concern in any handstand programming. Informing the user honestly that wrist pain is the most likely adverse outcome of this practice.
- Does not support
- That wrist warm-ups, braces, or volume management reduce wrist pain — this study looked for those associations (training hours p=.455, warm-up p=.171, brace use p=.418, grip device p=1.000, experience p=.758) and found none. No clinical exam or imaging was performed. Cross-sectional design — no causation.
E3Verified Pooled across 25 studies (185,107 adolescent artistic gymnasts): 53% wrist-pain prevalence, 36% chronic wrist injury. Increased training intensity is associated with wrist injury (AOR 1.19, p=.04) in one constituent study.
- Supports
- Wrist load is a genuine, high-prevalence risk in weight-bearing-on-hands practice across populations. Training intensity is plausibly implicated.
- Does not support
- Transfer to adults — this is an adolescent population with open growth plates, a distal-radial physeal stress-injury mechanism adults do not share. The review is "limited by the inclusion of studies with high risk of bias" and heterogeneous definitions, and explicitly failed to link physeal stress injury to positive ulnar variance. Conflicts with E2 (no volume association found in adults) — not resolved; both are kept because the populations, designs, and exposure measures differ.
E4Verified Distributing 20 minutes of practice into ten 2-minute bouts with rest beat one continuous 20-minute block for a speed-stacking motor skill, with the in-training advantage appearing only in session 1 and sessions 8-10 — not sessions 2-7.
- Supports
- Breaking a fixed practice budget into short bouts with rest, rather than one continuous block. Expecting the benefit to be visible early and late while flattening mid-learning — useful to tell a user who feels stalled mid-progression.
- Does not support
- That daily practice beats thrice-weekly practice by itself — this study distributed practice WITHIN a single session, not across days. The across-day evidence it cites (Bloom & Shuell 1981; Spruit, Band & Hamming 2014) is adjacent-domain (vocabulary, laparoscopic training), not a movement-skill study in trained adults. The task here was speed stacking — fine-motor sequencing, not whole-body balance under load. Transfer to handstand practice is an inference, not a finding.
E5Coaching only Handstand acquisition timelines vary by an order of magnitude: wall-supported hold within 2-4 weeks; freestanding 5-10s at 2-4 months; a 30s freestanding hold anywhere from 4-12 months; overall 3-12 months typical, 6-8 weeks for well-prepared trainees, multiple years for others.
- Supports
- A fixed calendar script is the wrong model. Progression must gate on demonstrated capacity, not elapsed days. A 365-day horizon is a reasonable envelope, not a schedule.
- Does not support
- Any of these figures as a norm. These are coaching observations, not measured cohorts — no confidence intervals, no controlled comparison, selection bias throughout. Treat as expectation-setting, never as a benchmark the user is failing to meet. No controlled trial of handstand acquisition exists at all.
GMB Fitness — handstand training guideCalisthenics Association — Handstand Training: The Complete GuideRead by a person on July 31, 2026E6Verified In practice, deloads last 6.4 ± 1.7 days and recur every 5.6 ± 2.3 weeks, reducing volume/intensity while holding frequency constant. However, a one-week deload at the midpoint of a 9-week program negatively influenced lower-body strength, with no effect on hypertrophy, power, or local muscular endurance.
- Supports
- Scheduling planned lighter weeks as a fatigue-management practice, holding frequency steady while reducing volume — this is what practitioners actually do.
- Does not support
- That deloads improve outcomes. One RCT found the opposite for strength. Any claim that a specific deload cadence is optimal.
E7Verified Proximity to failure, measured by reps-in-reserve, is real, graded, and produces measurably more fatigue closer to failure (velocity loss at 4min: failure -25%, 1-RIR -13%, 3-RIR -8%; n=24 trained lifters, bench press).
- Supports
- Justifies asking the user how close to failure a set felt, and justifies a level-up rule that requires reps in reserve rather than a maximal effort.
- Does not support
- That RIR is validated for novices — the RIR-velocity modeling study required >=6 months of resistance-training experience and states its findings "may not generalise" to those without it, and that less-experienced individuals had higher prediction error. That participants in the fatigue study actually hit their RIR targets accurately — the authors state this is unknown. Any bodyweight, isometric, or skill-work application — both studies are barbell lifts (bench press, back squat) at percentages of 1RM, where proximity to failure is confounded with technical breakdown rather than autoregulated against a known load. Design consequence: RIR cannot be the gate for progression in this app; it is usable only as a self-reported input and as confirmation-prompt wording.
E8Verified Novices told what to look for BEFORE watching a demonstration significantly outperformed those told after, on relative-timing accuracy at retention (p=.001, p=.02, n=90 and n=60). Doubling observation trials did not close the gap — "what has been learned in a FB protocol does not add up to what can be learned in a FW protocol."
- Supports
- Presenting technique checkpoints BEFORE the video rather than beside or after it. Direct justification for `formCriteria` existing as structured data rather than prose cues: the app can name what to watch for, then play the demonstration. Design consequence: a video link on its own is the weaker implementation — the session screen should show the checkpoints first, then the demonstration.
- Does not support
- Generalisation beyond novices — the authors explicitly limit the claim to novice observers and caution against extending it across expertise levels or task types. The task was a laboratory timing task (barrier-knockdown), not a compound bodyweight movement.
Observational Learning: Tell Beginners What They Are about to Watch and They Will Learn Better, 2016doi:10.3389/fpsyg.2016.00051Read by a person on July 31, 2026E9Verified An unskilled model (20min practice) beat both a skilled model (10 days practice) and a no-observation control on a novel ball-rotation task (p=.02, p=.03, n=36); a model slightly better than the learner may teach more than an expert model.
- Supports
- Caution against reflexively linking the most impressive demonstrator available. Model-learner similarity appears to matter; not acted on here (see the comment in content/movements/*.ts wherever a video is selected) — kept as a noted-but-unused consideration in case a future decision to swap in an elite demonstrator needs to weigh it.
- Does not support
- Direct transfer to calisthenics — n=36 on a fine-motor, non-dominant-hand ball-rotation task, not a compound bodyweight movement under load. Playback speed was not excluded as a confound. Not grounds for preferring unskilled demonstrators in this app; not acted on.
An effective model for observational learning to improve novel motor performance, 2016doi:10.1589/jpts.27.3829Read by a person on July 31, 2026E10Verified Exercise performance might be trivially reduced during the early follicular phase relative to all other phases. Because of that trivial effect size, large between-study variation, and the number of poor-quality studies included, the authors state that general guidelines on exercise performance across the menstrual cycle cannot be formed, and recommend a personalised approach based on each individual's own response across her own cycle.
- Supports
- Recording cycle phase alongside readiness and performance, and surfacing an individual's own pattern once enough cycles exist to show one. This is the approach the paper explicitly recommends, and it is the only one it licenses. Design consequence: a longitudinal personal record is not a nice-to-have here, it is the only defensible implementation.
- Does not support
- Every phase-based programming claim in popular circulation. It does not support prescribing lower intensity during menstruation, scheduling strength work into the follicular phase, deloading in the luteal phase, or any "cycle syncing" template — the finding is precisely that such general guidance cannot be derived from the current literature. It also says nothing about bodyweight or isometric work specifically, nothing about women on hormonal contraception (a separate review), and nothing about injury risk.
E11Verified Exercise reduces depression (SMD -0.61, 95% CI -0.69 to -0.54) and anxiety (SMD -0.47, 95% CI -0.59 to -0.36) symptoms. Aerobic exercise shows the largest effect. A separate umbrella review reports a number-needed-to-treat of 2.78 for depressive symptoms, and head-to-head and network comparisons generally show exercise, medication and psychotherapy with similar effect sizes in MILD cases.
- Supports
- The claim that a body action is also a mind action, which is why this product does not sort its domains by activity type — sorted that way the categories overlap exactly where they matter most.
- Does not support
- That exercise treats moderate or severe depression, or replaces care. The similarity to medication and psychotherapy is reported for MILD cases. It does not support any claim about this app specifically: none of these trials studied an app, a self-directed programme without supervision, or calisthenics in particular. 87% of the included meta-analyses were rated low or critically low quality on AMSTAR-2, and the umbrella review did not include head-to-head trials against pharmacotherapy or psychotherapy. It is not grounds for telling anyone to train instead of seeking help.
Effect of exercise on depression and anxiety symptoms: systematic umbrella review with meta-meta-analysis, 2025doi:10.1136/bjsports-2025-110301The efficacy of exercise interventions on depressive symptoms and cognitive function in adults with depression: an umbrella review, 2024doi:10.1016/j.jad.2024.09.074Read by a person on August 3, 2026E12Verified Mood monitoring and ambulatory assessment carry documented adverse events — increased burden or stress, mood worsening, self-harm and hospitalisation. Only 15 of 77 studies (19%) reported adverse events at all and only 3 (4%) used validated outcome assessments. Named mechanisms include monitoring acting as an unwelcome reminder of mental illness, rumination, perceived helplessness and intrusive reminders. Top barriers were technical issues (38%), being time-consuming (38%) and repetitive design (17%); the most requested improvement was personalisation and user control over timing (43%).
- Supports
- Refusing a standalone mood tracker. Capturing affect only when it is attached to an action and consumed by a decision — readiness on a session, distress on an exposure attempt — rather than on a schedule. Never prompting, never reminding, and never rendering an incomplete streak of readings.
- Does not support
- That mood monitoring is harmful on balance, or that nobody benefits: the same literature reports increased insight and relapse-prevention skills for some users, and the pooled adverse-event prevalence is low (0.04). The authors themselves state there is limited certainty in prevalence, duration and severity because of severe underreporting, heterogeneity and publication bias. It says nothing about non-clinical populations, and nothing about affect captured alongside an action rather than on a calendar — that design was not studied.
Adverse Events of Mood Monitoring and Ambulatory Assessment in Depression and Bipolar Disorder: Systematic Review and Meta-Analysis, 2025doi:10.2196/79500The user experience of ambulatory assessment and mood monitoring in depression: a systematic review and meta-synthesis, 2025doi:10.1038/s41746-025-02118-8Read by a person on August 3, 2026E13Verified In a one-year prospective cohort of 874 novice runners with GPS-measured distance, no statistically significant difference in overall injury rate was found between those who progressed weekly running distance by <10%, 10-30%, or >30%. A raised rate of DISTANCE-RELATED injuries specifically (patellofemoral pain, iliotibial band syndrome, medial tibial stress syndrome, gluteus medius injury, greater trochanteric bursitis, tensor fasciae latae injury, patellar tendinopathy) was seen in those progressing by more than 30% over a two-week period compared with less than 10% — hazard ratio 1.59, 95% CI 0.96 to 2.66, P = .07. The authors call the study exploratory, state that randomised trials are needed to verify it, and conclude that novice runners "may be well advised" to progress weekly distance by less than 30% over a two-week period.
- Supports
- A rate-of-increase cap on the running ladder, and the dwell floor derived from it: if no rung raises weekly distance by more than ~27% and no rung can be left in under two weeks, then no two-week window can contain a rise of 30% or more. That is the strongest rule this literature licenses, and it is a rule about VOLUME PROGRESSION RATE — not about technique, shoes, surfaces or stretching.
- Does not support
- The 10% rule, which this study specifically fails to support: <10% was not safer than 10-30%. Any claim that following the cap PREVENTS injury — the headline comparison was not statistically significant (P = .07, CI crossing 1) and the design was an exploratory cohort, not a trial. Anything about experienced runners (this was novices), about running speed or intensity (only distance was measured), about non-distance-related injuries (no association was found for those), or about any other sport.
Nielsen R.O., Parner E.T., Nohr E.A., Sørensen H., Lind M., Rasmussen S., Excessive Progression in Weekly Running Distance and Risk of Running-Related Injuries: An Association Which Varies According to Type of Injury, 2014doi:10.2519/jospt.2014.5164Buist I., Bredeweg S.W., van Mechelen W., Lemmink K.A.P.M., Pepping G.-J., Diercks R.L., No Effect of a Graded Training Program on the Number of Running-Related Injuries in Novice Runners: A Randomized Controlled Trial, 2008doi:10.1177/0363546507307505Read by a person on August 3, 2026
A machine checks the sources monthly for retractions and corrections. It never changes an entry: it raises the question, and a person decides what the change means.