Effects of a Resistance Training Program in Older Women With Sarcopenia: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Effects of a Resistance Training Program in Older Women With Sarcopenia (NCT02628145), a randomized na study. The primary outcome is Muscle Mass Change: From Dual Energy X-ray Absorptiometry and Bioelectrical Impedance Analsysis - Appendicular Lean Mass (ALM in kg) Divided by Height (Meters-squared).

2. Clinical Question

The trial asks whether a periodized resistance-training program is associated with a different change in appendicular lean mass relative to height than an active-control program in older women identified as presarcopenic or sarcopenic. The primary outcome is the mean change in appendicular lean mass divided by height squared, expressed in kg/m2, at the 12-week endpoint. The registry also lists measures of mobility, hip bone mineral density, strength, balance, gait speed, chair-stand time, and sarcopenia status.

This is a question about the results recorded for this trial, not a recommendation about exercise or treatment. The registry’s posted primary comparison is a mean difference between the two groups. Interpretation depends on the estimate, its uncertainty, the analysis used, and the limited amount of outcome information recorded.

3. Trial Design

The registry describes a randomized, parallel-group clinical trial with no masking. The two behavioral interventions were a resistance-training program and an active-control program involving light physical activity and stretching. The sponsor was the University of Rhode Island. The record lists the trial as completed, with a start date of 2015-08 and primary completion in 2016-06.

The enrollment field records 25 participants. The brief summary describes an intended total of 24 free-living older women, while the primary endpoint results list 12 participants in the resistance-training group and 10 in the active-control group. The adverse-event record lists 13 participants at risk in the resistance-training group and 12 in the active-control group. These figures refer to different registry entries; participant flow and reasons for the differences are not reported in the registry record.

The resistance-training sessions were scheduled three times per week on non-consecutive days for approximately 12 weeks, with 8-10 exercises for major muscle groups using free weights and machines. The active-control group was scheduled to meet three times weekly for light physical activity and stretching over approximately the same period. The summary says outcomes were collected at baseline, 6 weeks, and after the intervention. The primary outcome timeframe is 12 weeks.

Random allocation supports a comparison between groups, but the record does not describe the allocation sequence or concealment procedures. With no masking, participants and intervention staff would know which activity program was assigned; whether outcome assessors were masked is not reported in the registry record. The full protocol, detailed participant flow, and the trial’s original sample-size rationale are also not reported in the registry record.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Overall Study

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

6. Primary Endpoint

The registry lists the primary outcome as Muscle Mass Change: From Dual Energy X-ray Absorptiometry and Bioelectrical Impedance Analsysis - Appendicular Lean Mass (ALM in kg) Divided by Height (Meters-squared), measured over 12 weeks.

The primary endpoint is change in appendicular lean mass relative to height squared. Appendicular lean mass is defined in the registry description as the sum of non-bone lean mass in both arms and both legs. Dividing by height squared expresses that measure relative to body stature, rather than treating the raw amount of lean tissue as independent of body size. This kind of normalization is a general approach for making body-composition measures more interpretable across people of different heights; it does not establish that the measure captures every aspect of muscle health.

The registry describes body composition assessment using dual-energy x-ray absorptiometry, or DXA, and bioelectrical impedance analysis in the endpoint title. Its measurement description details DXA using fan-beam technology on a GE Lunar iDXA machine. Participants were tested in a fasted state, wore surgical scrubs, and were positioned using standardized procedures; a licensed radiology technician performed the tests. The description also says that appendicular lean mass, total body fat mass, and percent fat were measured.

The reported unit is kg/m2, and the endpoint timeframe is 12 weeks. A continuous mean outcome allows the group result to be expressed as an average and the difference between groups to be estimated. The registry does not report a threshold for a meaningful change in this measure, so the statistical estimate alone does not establish the practical or clinical importance of any difference.

7. Results Posted in the Registry

• Resistance Training Intervention: mean 0.09 versus 0.10 on control; difference -0.01 (95% CI -0.25 to 0.23), standardized effect d = -0.04; z-test p = 0.934.

8. Secondary Efficacy Endpoints

The registry also posts results for secondary outcomes. For each outcome below, the endpoint type, the test applied to the posted summary statistics, the result and its interpretation are given in turn. Secondary endpoints are usually not adjusted for multiple testing, so they support rather than confirm the primary finding.

Mobility Change: 8 Foot Timed up and go From a Seated Position Around a Cone Back to a Seated Position

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard errors.
• Result:
  • Resistance Training Intervention: mean -0.48 versus -0.74 on control; difference 0.26 (95% CI -0.46 to 0.98), standardized effect d = 0.30; z-test p = 0.480.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Resistance Training Intervention and the control. The interval gives the range of effects that remain compatible with the data.

Hip Bone Mineral Density: Measured by Dual Energy X-ray Absorptiometry

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Resistance Training Intervention: mean -0.00 versus 0.01 on control; difference -0.01 (95% CI -0.05 to 0.02), standardized effect d = -0.28; z-test p = 0.546.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Resistance Training Intervention and the control. The interval gives the range of effects that remain compatible with the data.

The registry identifies secondary outcomes spanning sarcopenia status, balance, mobility, hip bone mineral density, gait speed, grip strength, leg-press strength, and chair-stand time. The record also includes numeric comparisons for mobility and hip bone mineral density. Across those available comparisons, the recalculated uncertainty intervals include zero, and the registry-reported p-values do not indicate a statistically notable group difference. The numeric details for each outcome are reported with the endpoint results and need not be repeated to interpret the broader pattern.

The secondary outcomes measure different aspects of physical function and body composition, so they do not all answer the same question as the primary lean-mass endpoint. Mobility and bone density can complement a body-composition measure, but a result on one endpoint does not directly establish a result on another. The lack of a clear difference in the available secondary comparisons does not confirm the primary result, and it does not resolve the primary endpoint’s uncertainty.

Secondary findings generally carry less confirmatory weight when a trial assesses multiple outcomes without a reported testing strategy. Each additional test creates another opportunity for a result to appear notable by chance. The registry record does not report a multiplicity adjustment, a hierarchy of outcomes, or which secondary measures were intended as confirmatory. The listed secondary p-values should therefore be interpreted cautiously and not treated as independent proof of an effect.

The record indicates nine posted secondary outcomes, but detailed numerical results for all of them are not present in the information recorded for this analysis. Their directions, magnitudes, uncertainty, and missingness cannot be inferred from the outcome names alone. A broad conclusion about every secondary measure would go beyond the numeric evidence recorded. The defensible overall reading is limited to the outcomes with posted comparisons and the registry’s stated list of measures.

Secondary outcomes registered for this trial, for reference (only those above were recalculated):

• Sarcopenia Status Change
• Balance Ability: Single-leg Stand. Scored Yes or No
• Mobility Change: 8 Foot Timed up and go From a Seated Position Around a Cone Back to a Seated Position
• Hip Bone Mineral Density: Measured by Dual Energy X-ray Absorptiometry
• Physical Functioning Change: Normal Gait Speed Time From 400-meter Walk
• Grip Strength Change: From Hand Grip Dynamometry in kg
• Muscle Strength Change: Leg Press One-repetition Maximum in kg
• Chair Stand Time Change: Time to Complete Five Chair Rises From a Normal Chair

9. Statistical Interpretation

10. Statistical Methods Explained

The following explains the statistical ideas used to read the posted estimates. General statistical explanations are distinguished from details the registry reports about this trial.

What does a mean difference describe?

A mean is the average value of a continuous outcome within a group. For the primary endpoint, the registry reports a mean change for each group and a mean difference comparing the resistance-training group with the active-control group. The recalculated difference is defined as resistance training minus active control. A negative value therefore indicates that the resistance-training group’s mean is lower than the active-control group’s mean on the recorded change measure. The sign does not by itself indicate whether the difference is beneficial or important; that requires knowing how the measure relates to the question and what size of change matters.

The registry’s sponsor-reported primary analysis is described as a mixed models analysis of the mean difference in final values. A mixed model is a general statistical approach that can represent relationships among repeated measurements and account for structured data. The registry record does not give enough detail to reconstruct the specific model, including its fixed effects, covariance structure, or handling of missing observations. It is therefore not possible to determine those choices from the record.

What is the role of standard error?

The primary group results are reported as means with standard errors. A standard error describes the estimated uncertainty in a sample mean, conditional on the statistical framework used; it is not the spread of individual participant measurements. A standard deviation, by contrast, describes variation among individual observations. Confusing these quantities can make a group’s variability appear much smaller or larger than it is.

The primary outcome and mobility outcome list standard errors as their dispersion measure. The hip bone mineral density outcome lists standard deviations. Those summaries are not interchangeable. General statistical practice often uses an estimated standard error to construct an interval around a mean, but the recalculated comparisons depend on the posted summary statistics and should be distinguished from the sponsor’s model-based analysis.

What does a confidence interval add?

A confidence interval describes the uncertainty around an estimated effect under a specified method. In repeated use of the same method under its assumptions, intervals at a stated confidence level would cover the underlying parameter at the stated rate. It is not a probability statement that the particular fixed parameter lies inside the particular observed interval. For the primary recalculation, the interval extends from -0.246 to 0.226. Because it includes zero, the posted summary statistics are compatible with no difference as well as with differences in either direction within that interval.

The width of an interval matters as much as whether it includes zero. A wide interval allows a broad set of effects and indicates limited precision. A point estimate alone can conceal that uncertainty. The sponsor’s primary result does not have a confidence interval recorded, so the interval from the unadjusted recalculation should not be attributed to the mixed-model analysis.

What does a p-value mean?

A p-value is calculated under a statistical model and a null hypothesis. It quantifies how extreme the data, or data at least as extreme, would be under that hypothesis and model. It is not the probability that the null hypothesis is true, the probability that chance alone caused the result, or a measure of the probability that an intervention has an effect. Nor does it measure clinical importance. A small p-value does not establish importance, and a larger p-value does not establish equivalence.

The recalculated unadjusted primary p-value is 0.934, while the sponsor’s mixed-model result reports 0.91. The registry does not report the complete model specification or all analysis details needed to explain the difference. The sponsor’s estimate and p-value should be kept distinct from the unadjusted recalculation rather than combined as though they came from one model.

Why can repeated measurements and mixed models matter?

When outcomes are collected more than once for the same participant, measurements from that participant are generally related. A mixed model can be used to represent this within-participant relationship while estimating group effects. That is a general explanation; the registry indicates that a mixed models analysis was used for the primary comparison but does not describe its implementation. The summary identifies baseline, 6-week, and post-intervention measurement occasions, but the sponsor analysis is labeled as a comparison of final values. Details of how the repeated observations entered the model are not reported in the registry record.

It is also important that the published summary statistics and the sponsor’s model may answer related but not identical statistical questions. The recalculation uses simple unadjusted comparisons from the posted arm summaries. The sponsor analysis is explicitly described as a mixed-model analysis. Differences in adjustment, model specification, and handling of repeated measurements can affect standard errors and p-values, but the registry does not report enough detail to identify which features account for the values in this trial.

Why does over-dispersion matter in general?

Over-dispersion is a general concern for outcomes whose observed variability exceeds what a statistical model assumes. If a model understates variability, its standard errors can be too small and its intervals too narrow. If variability is represented more appropriately, uncertainty estimates may change. The primary endpoint is a continuous measure, and the registry does not report an over-dispersion assessment or identify over-dispersion as an issue. This concept should not be interpreted as a specific finding about this trial.

How should unadjusted secondary tests be read?

Each additional outcome can bring another opportunity to observe an apparently notable result by chance. When many outcomes are tested, a multiplicity strategy may be used to manage the overall error rate or to distinguish confirmatory outcomes from exploratory ones. The registry record does not report whether the secondary analyses were adjusted for multiplicity, which outcomes were prespecified as confirmatory, or how any hierarchy was defined. The secondary p-values should therefore be treated as unadjusted evidence unless the sponsor’s analysis information indicates otherwise; that additional detail is not reported.

These methods explanations clarify what the posted statistics can and cannot show. They do not fill gaps in the trial’s analysis record. The original protocol, statistical analysis plan, missing-data methods, and participant-level results are not reported in the registry record.

11. Confidence Intervals and Precision

The primary recalculated mean difference is -0.01 kg/m2, with a 95% confidence interval from -0.246 to 0.226. The interval is much broader than the point estimate and crosses zero. That pattern means the point estimate is close to no difference, but the data are not precise enough to restrict the plausible range to values close to that estimate alone. Both negative and positive differences remain compatible with the interval.

The sponsor’s mixed-model analysis reports a mean difference of -0.01 and a p-value of 0.91, but the registry record does not report an interval around that estimate. The recalculated confidence interval is based on the simple unadjusted summaries, not on the sponsor’s mixed model. The plotted uncertainty should likewise be interpreted according to the method used to produce it rather than assumed to reproduce the sponsor’s model.

Confidence intervals are more informative than a binary significant/not-significant label because they display both the estimated direction and the range of effects compatible with the data under the method. An interval that crosses zero does not prove no difference, and it does not prove equivalence. Equivalence requires a prespecified margin and an analysis designed to assess whether the interval lies within that margin; such a margin or equivalence analysis is not reported in the registry record.

Precision depends on the amount and variability of the data as well as the analysis. The primary endpoint results list 12 participants in the resistance-training group and 10 in the active-control group, and the group standard errors are 0.08 and 0.09. The relatively small recorded endpoint groups and the width of the interval make uncertainty central to interpretation. The registry does not report enough information to assess whether missing outcomes, exclusions, or model choices further affected precision.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The planning figures are illustrative sample sizes per arm for a two-group comparison, not the trial’s original design calculation. The assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect targeted in each row is a stated fraction of the observed effect. The rows show planning for 100%, 75%, and 50% of the observed effect, with separate columns for participants per arm for 80% power and participants per arm for 90% power.

For the primary outcome, planning for 100% of the observed effect gives 12,353 participants per arm for 80% power and 16,537 participants per arm for 90% power. Planning for 75% of the observed effect gives 21,961 and 29,399 participants per arm, respectively. Planning for 50% of the observed effect gives 49,411 and 66,147 participants per arm, respectively. These figures are illustrations derived from the observed estimate, not the sample-size justification for this trial.

The 80% power column represents the planned number per arm under the stated assumptions for a design with an 80% probability of detecting the targeted effect using the specified test when that effect is the true one. The 90% column describes the corresponding planning target at 90% power. A higher power target requires more participants under otherwise identical assumptions. Smaller effects require more participants because they are harder to distinguish from random variation.

The numbers are participants per arm, not total events. The assumptions underlying the trial’s original design are not reported in the registry record. These calculations are not observed power: they do not tell how much power the completed trial had after observing its data. Because the observed effect is close to zero, planning directly from it produces very large illustrative sample sizes; that feature does not establish that the observed effect is the true effect or the effect future research should target.

13. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = -0.010; pooled standard deviation σ = 0.281.
2. n = 2 × (1.96 + 0.842)² × 0.281² / -0.010² = 12,352.6, rounded up to 12,353 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
delta <- -0.01                      # observed difference in means
sigma <- 0.280517379140758                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(2628145)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 12,353 (80% power), 16,537 (90% power)
 75% of observed effect: n per arm = 21,961 (80% power), 29,399 (90% power)
 50% of observed effect: n per arm = 49,411 (80% power), 66,147 (90% power)
power.t.test: 12353.5 
Simulated power at n = 12,353 per arm: 0.798 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Analyses Reported by the Sponsor

The sponsor’s primary result is a mixed-model mean difference in final values of -0.01, with a reported p-value of 0.91. The unadjusted recalculation from the posted arm summaries also gives a mean difference of -0.01, but its p-value is 0.934 and its 95% confidence interval is -0.246 to 0.226. The estimates agree at the displayed precision, while the p-values are not identical.

These are related but distinct analyses. The sponsor’s result is the trial’s reported analysis and takes precedence when describing the sponsor’s conclusion from its model. The recalculation is a simple, unadjusted analysis of the posted summary statistics; it is useful as a transparent check but does not reproduce the mixed model. No discrepancy is flagged in the registry data. The difference between the p-values should not be treated as evidence of a substantive conflict.

The sponsor’s record does not include a confidence interval for the reported estimate. The interval from the recalculation therefore cannot be attached to the sponsor’s p-value or used to reconstruct the sponsor’s model. Details of the mixed-model specification, adjustments, and missing-data handling are not reported in the registry record. Those omissions limit further comparison between the analyses.

The most direct reading is that the recorded sponsor estimate is close to zero and its reported p-value does not indicate a statistically notable difference under that analysis. The unadjusted recalculation likewise has an interval that includes zero. Neither result alone establishes equivalence or a lack of any meaningful difference.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study evaluates several outcomes, time points, or comparisons. Even when no real group differences exist, testing many hypotheses can increase the chance of at least one apparently notable result. A prespecified strategy may control that risk, define one primary endpoint, arrange outcomes in a hierarchy, or distinguish confirmatory from exploratory analyses. The registry identifies a primary outcome and lists secondary outcomes, but a multiplicity strategy is not reported in the registry record.

Without a reported strategy, the secondary p-values cannot be interpreted as though each were the only test undertaken. They may be useful as descriptive or exploratory results, but the record does not establish how they were selected, whether all planned outcomes are reported, or whether adjustments were applied. The primary endpoint remains the clearest stated focus, while the secondary outcomes should be considered with added caution.

The record also does not describe missing-data methods, the analysis population, or how participants who did not complete all assessments were handled. It gives the enrollment figure, endpoint arm counts, and separate adverse-event denominators, but does not explain their relationship through participant flow. The brief summary names baseline, 6-week, and post-intervention assessments, while the primary sponsor analysis is labeled as a final-values comparison. How incomplete repeated measurements were handled is not reported in the registry record.

Randomization helps make groups comparable in expectation, but missing outcome data can weaken that protection if the likelihood of missingness relates to group assignment or outcome. This is a general concern, not a claim that such bias occurred in this trial. The record does not report reasons for withdrawal, completeness by outcome and time point, or sensitivity analyses for missing data. Nor does it describe whether the primary analysis followed an intention-to-treat principle or another analysis population.

These reporting gaps limit assessment of robustness. They do not show that the analysis was necessarily inappropriate; they mean that important aspects of the analysis cannot be checked from the registry record. The protocol and statistical analysis plan are not reported in the registry record.

16. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0% reporting threshold.

The adverse-event record lists 13 participants at risk in the resistance-training group and 12 in the active-control group. It records zero serious adverse events in each group, zero other adverse events in each group, and zero deaths in each group. These figures describe the events recorded in the registry for the stated groups and denominators.

A recorded zero is not proof that no event occurred outside the period, definitions, or reporting process captured by the record. The registry does not list serious adverse-event terms or explain how events were collected, defined, or followed over time. It also does not report whether all participants completed safety follow-up. These limits matter when interpreting any adverse-event summary, particularly when group sizes are small.

The adverse-event denominators differ from the primary endpoint group counts. Participant flow and the reason for that difference are not reported in the registry record, so the safety figures should not be substituted for the endpoint sample sizes. The recorded adverse-event data are descriptive and do not establish comparative safety beyond the events and participants listed.

17. What the Result Does, and Does Not, Mean

The primary result describes a small estimated difference in mean appendicular lean mass relative to height between the two groups at the recorded endpoint. The recalculated estimate is -0.01 kg/m2, and the sponsor’s mixed-model analysis reports a mean difference of -0.01. The uncertainty around the recalculated estimate includes zero and spans values in both directions. The sponsor’s analysis does not have a confidence interval recorded in the registry.

These results do not establish that the interventions are equivalent, that the true difference is exactly zero, or that a meaningful difference is absent. A conclusion of equivalence would require a defined margin and suitable analysis, neither of which is reported in the registry record. The posted data also do not identify a threshold for what would count as a practically important change in the primary measure.

The trial evaluates a specific resistance-training program against an active-control program in older women identified as presarcopenic or sarcopenic. The results should be understood in that setting. The record does not provide detailed demographic or clinical characteristics that would support broader claims about other populations, settings, exercise programs, or durations. The trial’s size and the uncertainty in the estimate limit how narrowly the plausible group difference can be described.

Secondary outcomes cover function and body composition, but only some have detailed numerical comparisons recorded in the available data. Those comparisons do not remove the uncertainty in the primary result. In addition, the registry does not report a multiplicity plan, full participant flow, or details of missing-data handling.

The appropriate conclusion is therefore bounded: the registry records a near-zero primary point estimate, but the available results do not precisely rule out differences in either direction. This is a description of statistical evidence, not medical advice and not a claim that either program does or does not work.

18. Why This Trial Matters Statistically

This trial is statistically informative as an example of why an estimate, its uncertainty, and the analysis behind it should be read together. The primary point estimate is close to zero, yet the recalculated interval is broad enough to include both negative and positive differences. Reporting only a p-value or only the point estimate would conceal important information about precision.

The record also distinguishes a sponsor-reported mixed-model analysis from a simple unadjusted recalculation. Their primary estimates agree at the displayed precision, but their p-values differ. Keeping the methods separate avoids treating a recalculation as if it were the trial’s own model and makes clear why access to the analysis specification matters.

There are further statistical lessons in the trial’s structure. It is randomized and parallel-group, but unmasked; outcomes were scheduled at more than one time point; and the registry lists multiple secondary measures. Those features make the allocation process, repeated-measure analysis, outcome hierarchy, multiplicity strategy, and handling of missing data important for a complete appraisal. Several of these details are not reported in the registry record.

Finally, planning illustrations based on an observed effect are highly dependent on the estimate used. They can clarify how smaller target effects require larger studies, but they are not a replacement for the original design rationale and should not be mistaken for observed power. Here, the registry’s original sample-size assumptions are not reported. The trial thus illustrates both the value of transparent quantitative summaries and the limits imposed by incomplete reporting.

19. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

Interpretation is limited by the small endpoint groups listed in the registry and by uncertainty around the primary estimate. The registry enrollment figure, the brief summary’s intended total, the endpoint counts, and the adverse-event denominators do not match one another. The record does not provide a participant-flow account to explain those figures, so the amount or reasons for any loss between enrollment and outcome reporting cannot be determined.

The trial was unmasked. Participants and intervention staff would know the assigned program, although assessor masking is not reported in the registry record. This matters because the intervention involves activities that participants can recognize, and the record does not specify safeguards against assessment or reporting effects. This is a potential limitation in design interpretation, not evidence that bias occurred.

The primary outcome description names DXA and bioelectrical impedance analysis, while its detailed measurement description focuses on DXA. The relationship between the two measurement approaches in the posted endpoint is not explained. The record also does not report the full eligibility criteria, participant characteristics, protocol deviations, adherence, or reasons for missing observations.

The sponsor’s mixed-model specification, missing-data approach, analysis population, and original sample-size justification are not reported in the registry record. Nor is a multiplicity plan for the secondary outcomes. These omissions prevent a full assessment of the analysis assumptions and the confirmatory status of secondary findings. The available numeric secondary comparisons cover only some of the outcome list, limiting any synthesis across all listed measures.

These limitations constrain the certainty and scope of interpretation. They do not negate the reported results, but they leave important questions about precision, completeness, and generalizability unresolved.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Effects of a Resistance Training Program in Older Women With Sarcopenia — NCT02628145.
• Registry record last updated 2023-10-04; status last verified 2022-12.
• Results first posted 2023-10-04.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

NCT02628145 is a completed randomized, unmasked, parallel-group behavioral trial sponsored by the University of Rhode Island. It compared a resistance-training program with an active-control program of light physical activity and stretching in older women identified as presarcopenic or sarcopenic. The primary endpoint was change in appendicular lean mass divided by height squared at 12 weeks.

The sponsor reported a mixed-model final-values mean difference of -0.01 and p = 0.91. An unadjusted recalculation gives a mean difference of -0.01, a 95% confidence interval from -0.246 to 0.226, and p = 0.934. The interval includes zero and supports caution about the precision of the estimate. The registry does not report the sponsor’s confidence interval, full analysis specification, multiplicity plan, or original sample-size assumptions.

The posted results are limited by small endpoint groups and incomplete reporting of participant flow and missing-data handling. They describe this trial’s recorded comparisons and do not establish equivalence or clinical importance.