Orthotics in Ambulatory Cerebral Palsy: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Orthotics in Ambulatory Cerebral Palsy (NCT01527162), a randomized na study. The primary outcome is Walking Activity Levels.

2. Clinical Question

The clinical question concerns activity measured in everyday life, rather than a laboratory measure of walking performance. The StepWatch accelerometer was intended to record participants’ daily strides during each condition. Two secondary measures addressed physical activity and life habits. The registry record does not report a specific threshold for a meaningful change in strides or scale scores, nor does it describe how participants’ individual responses were expected to vary.

3. Trial Design

This completed study, titled “Orthotics in Ambulatory Cerebral Palsy,” was sponsored by Seattle Children's Hospital. The registry record lists random allocation, no masking, and a crossover model. Enrollment was 11. The study started in 2012-01, had primary completion in 2014-07, and is listed as completed. The phase is recorded as NA.

The two conditions were wearing a prescribed SAFO and not wearing the prescribed SAFO, each for 14 days. The primary outcome timeframe was the average of 5 days of the second week of each intervention. The registry record does not describe the order in which conditions were received, any washout interval, adherence monitoring, or whether the same participants completed outcome assessments in both conditions. It also does not report the original design assumptions or sample-size justification.

Because this is a crossover trial, each participant may contribute observations under both conditions, allowing a comparison within the same person. That is a general feature of crossover designs, not a detail confirmed about the analysis in this record. The posted summary lists 11 participants for each condition, but does not explain whether all participants contributed complete data to both conditions. The sponsor’s reported analysis is identified as Wilcoxon (Mann-Whitney); whether that analysis accounted for the crossover structure is not reported in the registry record.

The registry record lists three outcome measures and four analyses. It describes the primary measure as average total strides per day, with standard deviation as the measure of spread. Two secondary outcomes are listed: the Physical Activity Scale for Kids - Performance Version (ASKp) and the Assessment of Life Habits for Children (LIFE-H). Further details on allocation procedures, masking beyond the listed NONE, and analysis populations are 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.

Population: ages 3.0 to 5.8 years, mean age 4.3 years, spastic diplegia cerebral palsy, all wearing current AFO bilaterally to enhance walking activity

6. Primary Endpoint

The registry lists the primary outcome as Walking Activity Levels, measured over average of 5 days of second week of intervention.

The primary endpoint, “Walking Activity Levels,” is the average total number of strides per day. Activity was measured with the StepWatch accelerometer, which documents daily strides. The registry record defines the outcome timeframe as the average of 5 days of the second week of the intervention. The reported unit is average total strides/day.

This endpoint captures walking activity in participants’ daily lives during each condition. As a general statistical and measurement point, an activity measure recorded over several days can reflect actual day-to-day behavior more directly than a single observation, while still varying with the days sampled. The registry record does not describe how missing days were handled, whether the 5 measurement days had to be consecutive, or how device data were checked.

The posted means were 4660.0 strides/day while wearing the SAFO and 4897.0 strides/day while not wearing it. Standard deviations were 1421.0 and 1438.0, respectively. These values describe the observed groups’ average activity and spread; they do not by themselves establish the size or precision of a condition effect. The registry record does not state a threshold for a clinically important difference in daily strides, so the practical importance of any contrast cannot be assessed against a stated benchmark.

7. Results Posted in the Registry

• SAFO Not Worn: mean 4,897 versus 4,660 on control; difference 237.00 (95% CI -957.70 to 1,432), standardized effect d = 0.17; z-test p = 0.697.

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.

Physical Activity Scale for Kids - Performance Version (ASKp)

• 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:
  • SAFO Not Worn: mean 49.45 versus 51.08 on control; difference -1.63 (95% CI -12.48 to 9.22), standardized effect d = -0.13; z-test p = 0.768.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between SAFO Not Worn and the control. The interval gives the range of effects that remain compatible with the data.

Assessment of Life Habits for Children (LIFE-H)

• 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:
  • SAFO Not Worn: mean 5.11 versus 5.71 on control; difference -0.60 (95% CI -2.36 to 1.16), standardized effect d = -0.29; z-test p = 0.503.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between SAFO Not Worn and the control. The interval gives the range of effects that remain compatible with the data.

The two secondary outcomes address physical activity and life habits, extending the primary focus on walking activity. Their posted means and recalculated comparisons are accompanied by sponsor-reported rank-test p-values. Across these measures, the recalculated estimates are imprecise, and the registry record does not provide a consistent, detailed account of how the sponsor’s analyses relate to the crossover design. The secondary results therefore add context but do not resolve the primary-analysis discrepancy.

In broad terms, the secondary outcomes do not provide a clear, consistent signal that can be used to strengthen a conclusion from the primary outcome. They are different constructs and should not be treated as interchangeable with daily strides. A scale-based outcome may capture aspects of activity or participation not represented by accelerometer counts, but the registry record does not report thresholds for meaningful changes on either scale.

As a general statistical consideration, multiple outcomes and analyses create more opportunities for apparently notable findings. Unless multiplicity is handled through a prespecified plan, individual unadjusted p-values carry less weight as confirmatory evidence. The registry record does not report a multiplicity adjustment or a hierarchy for secondary outcomes. The secondary findings are therefore best understood as exploratory context rather than independent confirmation of the primary result.

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

• Physical Activity Scale for Kids - Performance Version (ASKp)
• Assessment of Life Habits for Children (LIFE-H)

9. Statistical Interpretation

10. Statistical Methods Explained

What do the reported means and standard deviations describe?

The primary outcome is continuous: it is measured as average strides per day. A mean describes the arithmetic average within a condition. The standard deviation describes how spread out individual observations are around that average. In the posted results, the mean was 4660.0 with a standard deviation of 1421.0 while wearing the SAFO, and 4897.0 with a standard deviation of 1438.0 while not wearing it. These summaries are descriptive; they do not show how observations were paired within participants or how the sponsor performed its analysis.

As a general point, a standard deviation describes variation among observations, whereas a standard error describes uncertainty in an estimated mean. They answer different questions. The posted recalculation gives standard errors of 428.4 and 433.6 for the primary condition means. Such quantities depend on assumptions about the data and design. Since the trial is described as crossover but the registry record does not state how pairing was handled, these unadjusted summaries should not be treated as a fully specified crossover analysis.

What does the mean difference represent?

The recalculated mean difference compares the condition means, with the not-wearing condition expressed relative to the wearing condition. The reported estimate is 237.0 strides/day. A positive estimate under this direction means the posted mean was higher in the not-wearing condition. It is a simple unadjusted recalculation from summary statistics, not a reported estimate from the sponsor’s own analysis. It does not account for information that is unavailable in the registry record, such as the within-participant covariance or any period and sequence effects.

As a general concept, an effect estimate is more informative than a test result alone because it gives the direction and scale of the observed contrast. The estimate should be read together with its confidence interval and the design details. Here the available recalculated contrast is not equivalent to the sponsor’s reported Wilcoxon (Mann-Whitney) analysis, for which the registry record provides a p-value but no estimate or interval.

What does a p-value say?

A p-value is a measure of how incompatible data are with a specified statistical null model, under the assumptions of the analysis. It is not the probability that the null hypothesis is true, and it does not measure the probability that the result occurred by chance in a broad, assumption-free sense. Nor does it indicate whether an effect is important to participants.

The recalculated primary p-value is 0.697. The registry’s sponsor analysis reports p < 0.05 for the primary outcome. These values come from analyses that are not reconciled in the registry record. The sponsor analysis is the registry-reported analysis, while the recalculation is an unadjusted comparison of posted summary statistics. The method’s statistical significance threshold is not reported as part of the sponsor’s analysis details.

Why does the crossover design matter?

In general, a crossover design can compare each participant under different conditions. If the same participants contribute data in both conditions, an analysis can use within-person contrasts, which may account for stable differences between participants. This requires the data and analysis to preserve the pairing. The registry record identifies the design as crossover but does not report the order of conditions, a washout interval, handling of period or sequence effects, or whether the sponsor’s analysis used paired data.

The listed Wilcoxon (Mann-Whitney) method is a rank-based comparison commonly used for two independent groups. The registry record does not explain why this method was listed for a crossover design or whether the method label fully describes the sponsor’s analysis. It would not be appropriate to infer from the label alone whether the analysis did or did not account for the actual design. This lack of detail is especially relevant when comparing the sponsor’s result with an unadjusted recalculation.

What is the role of the confidence interval?

As a general explanation, a confidence interval presents a range of estimates compatible with the data under the method’s assumptions. The recalculated primary interval is -957.7 to 1432.0 strides/day. It spans values in both directions and is broad relative to the point estimate. It therefore conveys substantial uncertainty about the size and direction of the unadjusted contrast. It is not a range that guarantees the true effect lies inside it, and its interpretation depends on the calculation and design assumptions.

All recalculated estimates in this analysis are simple unadjusted comparisons based on the posted summary statistics. Since the registry record indicates a discrepancy between the sponsor analysis and recalculation, the sponsor’s own analysis takes precedence when describing the trial’s reported inferential result. The recalculations can help readers understand the posted means and their approximate contrast, but they cannot substitute for missing design and analysis details.

11. Confidence Intervals and Precision

The recalculated primary mean difference is 237.0 strides/day, with a confidence interval from -957.7 to 1432.0. The interval is wide and crosses zero, meaning the summary-statistic comparison is compatible with values on either side of no difference. The point estimate alone should not be read as a precise estimate of the contrast. The interval also does not establish that all effects within its limits are equally plausible or clinically meaningful.

As a general explanation, confidence intervals describe uncertainty around an estimate under a specified statistical method and its assumptions. They do not guarantee that the true effect falls within the reported range. Here, the interval is part of an unadjusted recalculation, not the sponsor’s reported analysis. The registry does not provide a confidence interval for the sponsor-reported Wilcoxon (Mann-Whitney) result, nor does it describe how that test handled the crossover design.

The small enrollment and reported 11 participants per condition are relevant to precision, but the record does not give the original sample-size rationale or a clinically important difference. Consequently, it is not possible to judge the interval against a prespecified meaningful threshold. The confidence interval describes uncertainty in the recalculated comparison; it does not prove equivalence, rule out a meaningful effect, or resolve the discrepancy with the sponsor’s reported p-value.

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 sample-size illustrations express participants per arm for 80% power and participants per arm for 90% power. They are not total event counts because these outcomes are continuous, rather than time-to-event outcomes. The illustrations use a two-sided significance level 0.05, equal allocation between the two arms, and a normal approximation. They calculate planning scenarios using the observed effect or a stated fraction of that effect. The original trial’s own design assumptions and sample-size justification are not reported in the registry record.

The 80% power column gives the planned number of participants per arm under the stated assumptions for an analysis to have 80% power to detect the effect used in that scenario. The 90% power column gives the corresponding per-arm count for 90% power. Power is a design property under assumptions about the effect, variability, analysis, and significance level; it is not a measure of whether the trial’s result is true.

The rows for smaller fractions of the observed effect require more participants per arm. That pattern is expected in general: smaller differences are harder to distinguish from variability, so larger samples are needed to achieve the same target power. The observed-effect scenario should not be read as a recommended target effect; it is an illustration based on the effect estimated in this small study. These calculations are planning illustrations, not observed power.

Because the trial is crossover, readers should also note that the illustrations describe two-arm planning assumptions, while the registry record does not report the original design calculation or explain whether the planning model reflects the crossover structure. The figures can help show how target effect size affects sample requirements, but they do not reconstruct the study’s original rationale.

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 = 237.000; pooled standard deviation σ = 1429.525.
2. n = 2 × (1.96 + 0.842)² × 1429.525² / 237.000² = 571.1, rounded up to 572 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 <- 237                      # observed difference in means
sigma <- 1429.52527085043                     # 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(1527162)
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 = 572 (80% power), 765 (90% power)
 75% of observed effect: n per arm = 1,016 (80% power), 1,360 (90% power)
 50% of observed effect: n per arm = 2,285 (80% power), 3,059 (90% power)
power.t.test: 572.1 
Simulated power at n = 572 per arm: 0.802 (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 registry record reports a sponsor analysis using Wilcoxon (Mann-Whitney) for the primary comparison and gives p < 0.05. It does not include an effect estimate, confidence interval, or further test details for that result. The recalculation from the posted summary statistics gives a mean difference of 237.0 strides/day, a confidence interval from -957.7 to 1432.0, and an unadjusted p-value of 0.697.

These results disagree. The registry record does not explain why, and the method label alone is not enough to determine the source of the discrepancy. In particular, it does not clarify how the reported analysis addressed the crossover structure. The recalculation is a simple unadjusted comparison and is not a replication of the sponsor’s analysis. The sponsor’s own analysis takes precedence as the trial’s reported analysis; the recalculation should be treated as a separate descriptive check, not as a replacement result.

15. Multiplicity, Missing Data and Analysis Populations

The registry record lists three outcome measures and four analyses, including the primary outcome and two secondary outcomes. It does not report whether outcomes were prespecified in an analysis hierarchy, whether any adjustment was made for multiple testing, or how the additional analysis for LIFE-H should be interpreted. Without this information, the error rate associated with interpreting several tests together cannot be assessed from the record.

As a general concept, when many outcomes or analyses are examined, the chance of at least one apparently unusual result can increase. Multiplicity procedures can address that issue, but the choice depends on the study’s aims and analysis plan. The record does not describe such a procedure. Accordingly, the sponsor-reported p-values for secondary outcomes should not be treated as if they were adjusted confirmatory tests.

Missing-data procedures and analysis populations are also not reported in the registry record. It does not state whether all enrolled participants contributed data to every condition and outcome, how incomplete accelerometer records were handled, or whether any participants were excluded from particular analyses. Although 11 participants are listed in each primary condition, that does not by itself establish completeness or explain the participant-level data structure in a crossover study.

The record also does not report an intention-to-treat definition, a per-protocol population, or sensitivity analyses for missing observations. These omissions limit assessment of potential bias and reproducibility. They do not establish that missing data or multiplicity changed the results; they mean that the registry record does not give enough information to evaluate those issues.

16. Safety Results

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

Other (non-serious) adverse events

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

The registry lists zero serious adverse events among 11 participants in the SAFO-worn condition and zero among 11 in the SAFO-not-worn condition. It also lists zero other adverse events among 11 participants in each condition. Death counts are not reported in the registry record, and no serious adverse-event terms are listed.

These entries describe what was recorded in the registry; they do not establish that no adverse events of any kind occurred outside the recorded categories or observation period. With a small enrollment, zero recorded events also cannot characterize uncommon events precisely. The registry record does not provide further detail about safety definitions, collection procedures, or the period covered by adverse-event monitoring.

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

The posted data describe daily walking activity under two orthosis conditions in a small randomized crossover trial. The condition means were 4660.0 and 4897.0 average strides/day, and the recalculated unadjusted comparison has a broad confidence interval that includes values in either direction. This indicates uncertainty about the size and direction of that particular recalculated contrast; it does not establish equivalence between conditions.

The sponsor’s reported primary test is different: it gives p < 0.05, but no estimate or confidence interval. Since the registry record flags a discrepancy, the sponsor’s analysis takes precedence as the reported trial result. The record does not explain the discrepancy, and the recalculated summary comparison should not be substituted for the sponsor’s analysis. Neither a p-value alone nor the recalculated interval indicates whether a difference would matter to participants.

The registry does not report a threshold for a clinically important change in strides, a detailed crossover analysis plan, or the original sample-size justification. It is therefore not possible to judge the reported contrasts against a stated clinical benchmark or to determine from the registry record how the intended analysis handled the within-participant design.

These results apply to the outcomes and participants recorded in this trial. They do not establish what would happen in other populations, with different orthoses or wear schedules, or over other time periods. The appropriate reading is a description of the recorded comparisons, with substantial limitations in the available analysis details and a discrepancy between the sponsor result and the unadjusted recalculation.

18. Why This Trial Matters Statistically

This study raises an important statistical issue: a crossover design and the analysis method need to be interpreted together. In general, crossover studies can use within-participant comparisons, but the registry record does not say whether the sponsor analysis used that information or how it handled condition order and period. This matters because a simple comparison of condition summaries may not represent the same estimand or uncertainty as an analysis that uses participant-level pairing.

The difference between the sponsor-reported p-value and the unadjusted recalculation is another reason to distinguish an analysis result from a descriptive re-analysis. The record reports a statistically notable sponsor result, while the recalculation yields a different p-value and a wide interval. Without further analysis details, readers cannot identify the cause of the discrepancy. Clearly separating the two preserves the evidential limits rather than presenting one as a correction of the other.

The study also illustrates why effect estimates and uncertainty are important alongside tests of statistical significance. The sponsor result has no reported effect estimate or interval, while the recalculated contrast gives a scale and a range but does not reproduce the crossover analysis. Better reporting of the planned estimand, analysis population, handling of paired observations, missing data, multiplicity, and clinically meaningful thresholds would make results easier to assess and reproduce.

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.

The registry record leaves several trial-specific details unreported. It does not describe the sequence of the crossover conditions, any washout interval, adherence to the 14-day periods, or whether outcomes were complete for all participants in both conditions. Those details are relevant to interpreting a crossover comparison, but their absence does not show that the design or conduct was inadequate.

The record does not provide the original sample-size justification, a clinically important threshold for daily strides or scale scores, or a full statistical analysis plan. It also does not explain how the sponsor’s Wilcoxon (Mann-Whitney) analysis accounted for the crossover design or why its primary p-value differs from the simple recalculation. No sponsor-reported effect estimate or confidence interval is listed for the primary comparison.

Only 11 participants are reported per condition. The registry does not give participant-level observations, missing-data procedures, or analysis-population definitions, so the recalculation cannot account for pairing or investigate outliers and data completeness. The secondary-outcome record includes more than one reported analysis for LIFE-H and does not describe a multiplicity plan. These limitations constrain precision and interpretation, but the registry information alone cannot establish how much they affected any result.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Orthotics in Ambulatory Cerebral Palsy — NCT01527162.
• Registry record last updated 2021-06-16; status last verified 2021-05.
• Results first posted 2016-02-04.
• 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

NCT01527162 is a completed randomized crossover study sponsored by Seattle Children's Hospital. It enrolled 11 ambulatory children with cerebral palsy and compared wearing a prescribed SAFO with not wearing it, each for 14 days. The primary endpoint was average daily strides measured with a StepWatch accelerometer, using the average of 5 days of the second intervention week.

The sponsor-reported primary analysis is Wilcoxon (Mann-Whitney), with p < 0.05. A simple unadjusted recalculation from posted summary statistics gives a mean difference of 237.0 strides/day, a confidence interval from -957.7 to 1432.0, and p = 0.697. The record flags a discrepancy, so the sponsor’s analysis takes precedence; the record does not explain the difference. Two secondary outcomes are listed, but multiplicity handling, missing-data procedures, and detailed crossover analysis methods are not reported in the registry record.