Physical Activity Behavior Change for Older Adults After Dysvascular Amputation: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Physical Activity Behavior Change for Older Adults After Dysvascular Amputation (NCT02738086), a randomized na study. The primary outcome is Retention Rate.

2. Clinical Question

3. Trial Design

This was a randomized, single-masked, crossover study listed as a pilot. The registry gives an enrollment of 31 and marks the study as completed. The sponsor was the VA Office of Research and Development. The recorded start date was 2016-07-01 and the primary completion date was 2019-02-22. The registry does not report the identity of the masked party.

The two sequences differed in when participants received PABC. The Early PABC Intervention group had the intervention during the first 3 months and a non-exercise control phase during the second 3 months. The wait-list group had a non-exercise control phase first, then PABC in the second 3 months. Thus, each sequence included an intervention period, but the posted primary retention comparison is between the groups as labeled in the result.

The arm-level results list 16 participants in the early-intervention group, with 14 completing, and 15 in the wait-list group, with 13 completing. The registry does not describe a washout period, how possible period effects were handled, or whether the result was adjusted for the crossover sequence. Those design and analysis details are not reported in the registry record.

The study also listed accelerometer-based physical activity and the Late Life Function and Disability Scale as secondary outcomes. These outcomes cover activity and self-reported function or disability, but the record summarized does not include their result estimates. No formal trial phase applies in the registry entry, which lists phase as not applicable.

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 Retention Rate, measured over 3 months.

Retention rate was the primary endpoint. The registry defined it as the percent of participants enrolled in the intervention who completed the intervention, with a timeframe of 3 months. In the posted arm results, completion is represented by participant counts: 14 of 16 in the Early PABC Intervention group and 13 of 15 in the wait-list group.

Retention is useful in a pilot because it indicates whether participants remain engaged through the intervention period. For an intervention involving wearable sensors, a tablet, feedback, and therapist contact, completion is relevant to feasibility: participants must stay involved long enough to receive the planned intervention. Retention does not, by itself, establish whether participants increased physical activity, improved function, or experienced a lasting behavior change.

The endpoint also depends on how completion was defined and recorded. The registry supplies a general definition but does not explain the operational threshold for being counted as a completer, how withdrawals or missed sessions were handled, or whether every randomized participant was included in the retention denominator. The reported counts therefore describe the posted endpoint, while the detailed rules used to classify completion are not reported in the registry record.

7. Results Posted in the Registry

• Early PABC Intervention: 87.5% (14/16) versus 86.7% (13/15) on control; risk difference 0.8 percentage points (95% CI -22.8 to 24.5), risk ratio 1.01 (0.77–1.32); unadjusted two-proportion z-test p = 0.945.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary comparison is expressed as a risk difference. For a binary outcome such as completion, a risk difference describes the difference between the proportions completing in two groups, with the direction depending on which group is subtracted from which. A value of zero corresponds to equal observed proportions. The registry record gives an estimated risk difference and an interval, alongside the participant counts used for the comparison. Because the interval includes zero and reaches both positive and negative values, the data do not pin down the direction or size of a difference precisely.

What does the unadjusted test tell us?

The unadjusted p-value is 0.945. In general, a p-value measures how unusual data at least as incompatible with a specified null model would be if that model were true. It is not the probability that the null hypothesis is true, and it is not a measure of the probability that the result is due to chance. For this small pilot, it should be considered alongside the effect estimate, the interval, and the limited number of participants. The registry record does not describe an adjusted primary analysis or a different inferential model.

The posted comparison also reports a relative risk and an odds ratio. In general, the relative risk compares the probability of the event between groups as a ratio, while the odds ratio compares event odds. Ratios near one indicate similar observed relative event levels, but an interval around a ratio can be wide even when its point estimate is near one. Here, the reported intervals span values on both sides of one, so the relative comparisons are also uncertain. The risk difference may be easier to interpret in this setting because it expresses an absolute contrast rather than a ratio.

Why does the small sample matter?

With few participants, the observed proportions can shift noticeably when a small number of outcomes change. This makes the point estimate sensitive to individual completion classifications and typically leaves less information for estimating the underlying group difference. The wide interval is consistent with this limitation. A result that fails to show a clear difference is not equivalent to demonstrating equivalence; an equivalence question would require a prespecified margin and an analysis designed to assess that margin. Such a margin is not reported in the registry record.

The study is described as randomized and crossover. Randomization supports a comparison of assigned sequences, but crossover data can require consideration of treatment period and sequence, as well as the correlation between observations from the same participant. In general, accounting for these features can affect standard errors and estimates. The registry record does not report whether such a model was used for the retention comparison, or how the primary endpoint was analyzed in relation to the crossover design. The simple unadjusted recalculation is not a substitute for an unreported crossover-specific analysis.

How should the endpoint and other outcomes be distinguished?

Retention is a binary completion outcome in the posted results. It differs from accelerometer-based activity, which is a behavioral measure, and from the Late Life Function and Disability Scale, which assesses reported frequency or limitation. The record lists these secondary outcomes but does not provide their numerical results in the available results summary. Conclusions about retention should not be extended to those other domains.

More generally, statistical significance, effect magnitude, and precision answer different questions. The p-value addresses compatibility with a null model; the effect estimate describes the observed contrast; and the interval represents uncertainty in that estimate under the method used. None of these alone establishes practical importance or generalizability. The registry does not report a prespecified clinically important difference, a formal analysis plan, or details needed to assess whether all planned analyses were completed.

10. Confidence Intervals and Precision

The retention estimate is imprecise. The interval for the risk difference crosses zero and extends to values favoring either sequence. In practical terms, the posted data do not distinguish confidently between a small difference, no difference, or a difference in the opposite direction. The interval is broad relative to the point estimate, so the estimate should not be treated as a stable measure of the size of a retention effect.

The relative-risk and odds-ratio intervals are also wide and include the no-association value of one. This means that the data are compatible with a range of relative comparisons. The point estimates alone can give a misleading impression of certainty if the intervals are ignored. In a small pilot, uncertainty is expected to be substantial because the number of observed completion outcomes is limited.

A confidence interval, in general, is a range of estimates compatible with the observed data under a particular statistical method. It reflects sampling uncertainty, not every source of uncertainty. It cannot account automatically for issues such as outcome misclassification, incomplete follow-up, or model misspecification. The registry does not report enough detail to evaluate all of those possibilities or identify the exact method used to construct the posted interval.

The interval should also be read in the context of the crossover design. If period or within-participant dependence was not incorporated, the precision assessment could differ from one based on a crossover-specific model. The record does not report the analysis details needed to judge this. The safest reading is that the posted comparison is uncertain and descriptive for this pilot, rather than a precise estimate that can be transported directly to a larger population.

11. 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 participants per arm, not total events. They are illustrations based on the observed effect and do not reproduce the trial's original design calculation. The stated assumptions are a two-sided significance level of 0.05, equal allocation between two arms, a normal approximation, and an effect to detect set at the stated fraction of the observed effect. The trial's own original sample-size assumptions or justification are not reported in the registry record.

For each effect scenario, the 80% power column gives the number of participants per arm in a hypothetical future study designed to have an 80% chance of detecting an effect of that size under the stated assumptions, if the effect exists. The 90% power column gives the corresponding per-arm planning number for a higher chance of detection. These are design targets, not results from the completed pilot. The figures are 25,426 and 34,037 participants per arm for planning at 100% of the observed effect; 45,512 and 60,927 for planning at 75% of the observed effect; and 103,098 and 138,019 for planning at 50% of the observed effect.

Smaller effects are harder to distinguish from random variation, so the planning figures increase as the assumed effect becomes smaller. The estimates are especially sensitive when the observed effect comes from a small pilot and is uncertain. They should not be interpreted as a definitive recruitment recommendation. This is not observed power: it is a forward-looking planning illustration, not a measure of what the completed study achieved.

12. 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, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.867; treatment proportion p₁ = 0.875; average p̄ = 0.871.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4743 = 0.9296.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4743 = 0.3992.
4. n = (0.9296 + 0.3992)² / (0.0083)² = 25,425.3, rounded up to 25,426 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
p0 <- 0.866666666666667                          # control proportion
p1 <- 0.875                          # treatment proportion
n_per_arm <- function(power, frac = 1) {
  q1 <- p0 + (p1 - p0) * frac               # smaller effect = fraction of the observed difference
  pbar <- (p0 + q1) / 2
  z_b <- qnorm(power)
  ceiling(round((z_a * sqrt(2 * pbar * (1 - pbar)) + z_b * sqrt(p0 * (1 - p0) + q1 * (1 - q1)))^2 / (q1 - p0)^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 (unrounded n per arm)
cat("power.prop.test:", round(power.prop.test(p1 = p0, p2 = p1, power = 0.80)$n, 1), "\n")

# Simulation: how often does the z-test reject at the 80%-power sample size?
set.seed(2738086)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 25,426 (80% power), 34,037 (90% power)
 75% of observed effect: n per arm = 45,512 (80% power), 60,927 (90% power)
 50% of observed effect: n per arm = 103,098 (80% power), 138,019 (90% power)
power.prop.test: 25425.3 
Simulated power at n = 25,426 per arm: 0.798 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-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.

13. Multiplicity, Missing Data and Analysis Populations

The registry lists six secondary outcomes, including accelerometer-based physical activity and the Late Life Function and Disability Scale measures of frequency and limitation. The record also states that there are 10 outcome measures. Multiple outcomes create a multiplicity issue: when many hypotheses are assessed, the chance of at least one apparently notable result can increase. In general, investigators may address this through a prespecified hierarchy, adjustment, or a clearly exploratory interpretation. The registry record does not report a multiplicity strategy.

Although the primary retention comparison has a posted result, the record does not provide numerical results for the listed secondary outcomes in the results summary described. Nor does it report whether analyses were prespecified, how outcomes were selected for reporting, or whether any outcomes were omitted. Without those details, the secondary outcomes cannot be used to make a comprehensive claim about the intervention's activity or function results.

Missing-data handling is not reported in the registry record. The arm counts show the numbers assigned and the numbers recorded as completing, but they do not describe how missing observations were treated in the statistical comparison, whether participants with incomplete outcome data were included, or whether any imputation or sensitivity analysis was performed. For a retention endpoint, non-completion is itself relevant, but the record does not explain how withdrawals, missed contact, or unavailable measurements were classified.

Analysis populations are also not reported. The record does not say whether the primary comparison followed an intention-to-treat principle, included only participants who began the intervention, or used another set of participants. It does not describe exclusions after randomization. The crossover design raises additional questions about how observations across periods were handled, but the statistical model and treatment of within-participant data are not reported. Interim analyses and stopping rules are not reported in the registry record either.

14. 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.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: non-healing wounds (6.7%), cardiac disorder - other (6.2%), suicidal ideation (6.2%).

Serious adverse events were recorded by group and study period. The posted counts of participants affected by a serious event were 1 during Group 1's Early PABC Intervention period, 2 during Group 1's No Contact Phase, 1 during Group 2's PABC Attention Control period, and 0 during Group 2's PABC Intervention period. The corresponding numbers at risk were 16, 16, 15, and 15. Deaths were recorded as 0 in each of these periods.

Other, non-serious adverse events affected 8 participants in Group 1's early intervention period, 5 in its no-contact period, 8 in Group 2's attention-control period, and 7 in Group 2's intervention period. These are period-specific counts and should not be added across periods: the crossover sequences may include the same participants in more than one period. The record lists Non-Healing Wounds at 6.7%, Cardiac Disorder - Other at 6.2%, and Suicidal Ideation at 6.2% among the top serious-event terms. The registry does not provide enough detail in this summary to infer event attribution or compare risk causally between periods.

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

The posted primary result describes retention during a feasibility-oriented intervention study. Completion counts were 14 of 16 in the early PABC group and 13 of 15 in the wait-list sequence. The recalculated unadjusted comparison is not statistically compelling, and its interval is broad. This combination means that the record offers limited information about the magnitude of any retention difference.

The result does not show that the groups are equivalent. A non-significant comparison with an imprecise interval can occur when the study has little information to distinguish among several plausible effects. Nor does the result establish that PABC improves physical activity or function. Retention is an engagement measure; the listed activity and function outcomes address different questions, and their estimates are not reported in the record summarized.

The randomized crossover arrangement is relevant to how the comparison should be understood. The groups received PABC in different periods, and the registry does not explain how period effects or repeated observations were handled. The posted unadjusted comparison therefore should not be read as a full account of every design feature or as a definitive estimate for a larger, differently structured study.

In general, pilot results can inform the practical planning of later research, including attention to recruitment, completion, and measurement procedures. They are usually less suited to precise estimates of effects, particularly when group sizes are small. Here, the large uncertainty in the retention comparison and the absence of secondary outcome estimates limit broader conclusions. The posted result is best regarded as an initial description of completion in this study, not as a clinical recommendation or a definitive assessment of behavior change.

16. Why This Trial Matters Statistically

This trial raises several statistical issues that are common in behavioral interventions for clinical populations. Retention is a meaningful feasibility outcome, but it is not a substitute for measuring the behavior the intervention aims to change. Keeping those questions separate helps prevent a completion result from being overinterpreted as evidence about activity or function.

The crossover design also illustrates why design details and analysis details need to be considered together. When participants experience different conditions in different periods, comparisons may depend on treatment sequence, period, and correlation between observations from the same person. A registry entry that identifies a crossover model but does not report the analysis model leaves an important interpretive gap. Statistical precision can depend on those choices.

The small group sizes make uncertainty central. The result has a high unadjusted p-value and an interval that allows effects in either direction. Neither feature demonstrates the absence of a meaningful difference. The planning illustrations also show how sensitive future sample-size requirements are to the assumed effect: planning around a smaller fraction of the observed effect requires many more participants per arm. This is a general design lesson, not evidence that the original study was intended to test those effects.

Finally, the record lists multiple secondary outcomes but provides no estimates for them in the summarized results. That limits assessment of the wider research question and makes transparent reporting important: endpoint definitions, analysis populations, missing-data methods, and multiplicity plans help readers understand what was tested and how uncertainty was quantified.

17. 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.

The primary comparison is based on small groups, and the interval is wide. As a result, the estimated retention contrast is not precise. The study is described as a pilot, which further supports treating the findings as preliminary rather than as a definitive estimate.

The registry record does not report the analysis model used for the crossover design, including whether period, sequence, or within-participant dependence was accounted for. It also does not report a washout period or the operational details for defining intervention completion. These omissions make it harder to assess whether the posted comparison fully reflects the design.

Details about the analysis population, missing-data handling, and multiplicity are not reported. The listed secondary outcomes do not have numerical results in the summarized record, so the retention finding cannot be placed alongside estimates of activity or function. The registry does not report an original sample-size justification or the protocol assumptions used to plan the trial. The future planning figures are illustrative and should not be mistaken for the trial's own recruitment target or for evidence that the study had adequate power.

Finally, the target population was Veterans with lower limb amputation after dysvascular disease, and the record lists related conditions including type 2 diabetes mellitus and peripheral artery disease. The modest study size and specific population limit how confidently the retention counts can be generalized to other populations or intervention settings. These limitations do not invalidate the posted counts; they define the scope of what can be concluded from them.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: Physical Activity Behavior Change for Older Adults After Dysvascular Amputation — NCT02738086.
• Registry record last updated 2020-02-18; status last verified 2020-02.
• Results first posted 2020-02-18.
• 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.

21. Record Summary

NCT02738086 evaluated Physical Activity Behavior Change for older Veterans after dysvascular amputation. It was a completed, randomized, single-masked crossover pilot sponsored by the VA Office of Research and Development. The registry records enrollment of 31, with the study starting on 2016-07-01 and primary completion on 2019-02-22.

The primary endpoint was retention at 3 months. Completion was recorded for 14 of 16 participants in the early-intervention sequence and 13 of 15 in the wait-list sequence. The unadjusted recalculation reports p = 0.945, while the interval for the risk difference is broad and includes zero. The result is therefore uncertain and should be interpreted as a pilot description of retention rather than a precise estimate.

Secondary activity and function outcomes are listed, but their numerical results are not reported in the registry record summarized. Analysis details for the crossover design, missing data, and multiplicity are also not reported.