Locomotor Experience Applied Post Stroke Trial: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Locomotor Experience Applied Post Stroke Trial (NCT00243919), a randomized phase 3 study. The primary outcome is Percentage of Patients Who Successfully Improved Functional Level of Walking at 1 Year Post-stroke.

2. Clinical Question

The clinical question is about achieving a specified walking-speed category, not about the average change in walking speed. For a participant whose baseline speed was less than 0.4 m/sec, success meant walking greater than 0.4 m/sec. For a participant whose baseline speed was 0.4 m/sec or greater but less than 0.8 m/sec, success meant walking greater than 0.8 m/sec. The speed was measured during a 10 meter walk.

The registry lists three behavioral programs, randomized allocation, and a parallel model. Participants were assigned to early locomotor training, late locomotor training, or home exercise. The comparison therefore concerns the percentage meeting the defined success criterion in each group. The primary result does not report a continuous walking-speed change or a broader measure of recovery. The registry record does not report a primary endpoint definition for participants whose baseline speed was 0.8 m/sec or greater.

3. Trial Design

The LEAPS Trial was a randomized, parallel-group phase 3 study sponsored by Duke University. Its listed condition was stroke, and the registry reports enrollment of 408. The study start is recorded as 2006-04, primary completion as 2010-04, and status as completed. The registry describes the interventions as behavioral programs: early locomotor training, late locomotor training, and a Home Exercise Program.

The early and late locomotor programs are both described as body weight supported training with a treadmill. The home program is described as a non-specific low intensity exercise program. The registry records masking as none. The arm sizes reported for the primary endpoint are 139 for early locomotor training, 143 for late locomotor training, and 126 for home exercise. These are the endpoint analysis group sizes, not a replacement for the overall enrollment figure.

The primary outcome is the percentage of participants successfully improving their functional level of walking at 12 months post-stroke. The registry specifies an intention-to-treat analysis and says missing data were imputed using the LOCF method. The trial also recorded a 6-month walking improvement outcome, walking speed during a 10-meter walk, 6-minute walking distance, daily steps, Stroke Impact Scale domains, and the Fugl-Meyer Lower Extremity Score. The registry record lists 12 outcome measures and 23 analyses.

The registry record does not report the original sample-size justification, the trial's planned statistical analysis details beyond the stated primary analysis population and missing-data method, or whether interim analyses were planned or conducted. It also does not report further details about sequence generation or allocation concealment. Those omissions limit what can be concluded about the design and conduct from the registry record alone.

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.

Before assignment: Participants admitted for inpatient rehabilitation were screened by chart review. Eligible participants with first-time stroke received a comprehensive medical record review and physical and cognitive screening. At 2-months, those who maintained eligibility and successfully completed an exercise tolerance test were enrolled.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Intention to treat analysis. Missing data were imputed using the LOCF method.

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 Percentage of Patients Who Successfully Improved Functional Level of Walking at 1 Year Post-stroke, measured over 12 months post-stroke.

The primary endpoint is a percentage: the proportion of participants classified as having successfully improved their functional level of walking at 12 months post-stroke. The classification uses thresholds based on baseline walking speed, measured during a 10 meter walk. A participant starting below 0.4 m/sec had to walk greater than 0.4 m/sec to count as successful. A participant starting at 0.4 m/sec or greater but below 0.8 m/sec had to walk greater than 0.8 m/sec.

This outcome turns walking performance into a binary classification: each participant either meets the specified success rule or does not. A percentage makes the frequency of meeting that rule interpretable across the treatment groups. It does not describe how far a participant's speed changed, how close a participant came to a threshold, or whether changes below the threshold were meaningful. Two people with different speed changes can receive the same classification, and a small difference around a threshold can change classification.

The registry's primary endpoint is at 12 months, while a related endpoint assesses successful improvement at 6 months. The time point matters: a 6-month classification and a 12-month classification answer different questions about when participants meet the threshold. The registry record does not report additional detail about how the primary endpoint handles participants whose baseline walking speed was 0.8 m/sec or greater. The primary population is described as intention to treat, with missing data imputed using LOCF.

7. Results Posted in the Registry

• Late Locomotor Training Program: 53.8% (77/143) versus 50.4% (70/139) on control; risk difference 3.5 percentage points (95% CI -8.2 to 15.1), risk ratio 1.07 (0.85–1.34); unadjusted two-proportion z-test p = 0.558.
• Home Exercise Program: 51.6% (65/126) versus 50.4% (70/139) on control; risk difference 1.2 percentage points (95% CI -10.8 to 13.3), risk ratio 1.02 (0.81–1.30); unadjusted two-proportion z-test p = 0.842.

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.

Percentage of Patients Who Successfully Improved Functional Level of Walking at 6 Months Post-stroke

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Late Locomotor Training Program: 32.2% (46/143) versus 50.4% (70/139) on control; risk difference -18.2 percentage points (95% CI -29.5 to -6.9), risk ratio 0.64 (0.48–0.85); unadjusted two-proportion z-test p = 0.002.
  • Home Exercise Program: 49.2% (62/126) versus 50.4% (70/139) on control; risk difference -1.2 percentage points (95% CI -13.2 to 10.9), risk ratio 0.98 (0.77–1.25); unadjusted two-proportion z-test p = 0.851.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Late Locomotor Training Program than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Home Exercise Program and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover walking performance, daily activity, participation, activities of daily living, mobility, and lower-extremity function. The registry lists measures at 6 months as well as measures such as walking speed and walking distance. Taken together, they assess a broader set of functional domains than the primary binary walking-success endpoint. The registry reports 10 posted secondary outcomes, while listing 12 outcome measures overall.

The broad pattern is not uniform across time points and outcome types. The 6-month walking-success outcome has a different pattern of group comparisons from the primary 12-month outcome. This means the secondary findings should be understood as additional evidence about specific time points and measures, not as a replacement for the primary result. A difference on a secondary measure does not automatically establish a difference in the primary endpoint, and a non-significant primary comparison does not erase every secondary observation.

The registry record lists 23 analyses, indicating that the posted results involve multiple statistical comparisons. When many outcomes and contrasts are examined, some results may appear noteworthy by chance even if there is no underlying effect. The registry record does not report a multiplicity adjustment or a prespecified hierarchy for interpreting these secondary tests. Their p-values should therefore be treated as unadjusted unless the record states otherwise, and they carry less confirmatory weight than a single primary comparison with a prespecified analysis plan.

Secondary measures can still provide useful context: different measures may capture different aspects of function, and a binary threshold may not reflect the full range of change. However, without reported control of multiplicity and fuller details of the analysis plan, the secondary pattern is best regarded as exploratory or supportive rather than decisive. The record does not report enough information to establish which secondary analyses were designated as confirmatory in advance.

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

• Percentage of Patients Who Successfully Improved Functional Level of Walking at 6 Months Post-stroke
• 6 Month Outcome: Walking Speed: Measured During a 10-meter Walk
• 6 Minute Walking Distance (Meters)
• Step Activity Monitor (SAM)- Median of Average Number of Steps Per Day
• Stroke Impact Scale (SIS) - Participation
• Stroke Impact Scale (SIS) - Activities of Daily Living/Instrumental Activities of Daily Living (ADL/IADL)
• Stroke Impact Scale (SIS) - Mobility
• Fugl-Meyer Lower Extremity Score

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is binary at the participant level: success is defined by meeting the specified walking-speed threshold, and the reported outcome is the percentage classified as successful. A comparison of percentages can be expressed in different ways. The unadjusted re-calculations use a risk difference, which describes the difference between the two percentages as a proportion. A value of zero represents equal percentages; positive or negative values indicate the direction of the difference according to the comparison order. The posted risk-difference confidence intervals cross zero for both primary re-calculations.

What does a risk difference describe?

A risk difference keeps the comparison on the percentage scale and is often straightforward to interpret as an absolute contrast. Here, it is based on the observed counts and group sizes for participants meeting the primary success definition. The re-calculations are simple, unadjusted comparisons from the posted summary statistics. They do not account for covariates or use the sponsor's regression model. The registry record does not report covariate details for the sponsor's primary logistic-regression analyses.

Other measures for binary outcomes include the risk ratio and odds ratio. A risk ratio compares the event proportions as a ratio. An odds ratio compares the odds of the event between groups; odds are not the same quantity as probability. The posted re-calculations include these measures, but the main interpretation above emphasizes risk differences because they express an absolute percentage-point contrast in the outcome scale. The sponsor's reported analyses use odds ratios from logistic regression. An odds ratio should not be read as a risk difference, and the numerical values of these measures are not interchangeable.

What does logistic regression contribute?

Logistic regression is a model for a binary outcome. It represents the relationship between predictors and the log odds of the event, and commonly reports an odds ratio for a contrast between groups. The registry identifies the method as logistic regression and reports odds ratios, confidence intervals, and p-values for the listed group comparisons. The registry record does not report which covariates, if any, were included, how the model was specified, or whether any adjustments were made. The model's reported result should therefore be described as the sponsor's logistic-regression analysis without assuming unreported model details.

The re-calculations and the sponsor's analyses differ in both effect measure and comparison structure. The re-calculations compare late training with early training and home exercise with early training using unadjusted risk differences. The sponsor analyses compare early training with home exercise and late training with home exercise using logistic-regression odds ratios. Because the reference groups and effect measures differ, the estimates cannot be directly treated as duplicate versions of the same quantity. When a discrepancy is flagged, the sponsor analysis takes precedence; no discrepancy is flagged in this record.

How should p-values be read?

A p-value describes how compatible the observed data are with a specified 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 size or clinical importance of an effect. The unadjusted primary p-values are 0.558 and 0.842. The sponsor's primary p-values are 0.481 and 0.501. Those values do not replace the effect estimates or confidence intervals. A result with a p-value above a conventional threshold is not proof that groups are identical; it can also reflect uncertainty or limited information for distinguishing a difference.

Likewise, a p-value below a threshold does not by itself establish that a difference is important or that it is free of bias. The registry's 6-month sponsor analyses report p-values of 0.010 and 0.007. They concern a secondary time point and should be interpreted in that setting, including the number of outcomes and analyses being considered.

Why is over-dispersion not the issue for this endpoint?

Over-dispersion matters for some count or clustered-data models when observed variability exceeds the variability expected under the assumed model. The primary outcome is reported as a percentage of participants meeting a binary definition, and the posted comparisons use binary-outcome measures. The registry record does not identify an over-dispersion model or report a count-model analysis. It would therefore be inappropriate to claim that over-dispersion was assessed or that a particular correction was applied. More generally, statistical methods need to match the outcome structure and design; extra modeling assumptions cannot be inferred from a reported percentage alone.

The registry names intention to treat as the primary analysis population and LOCF as the missing-data approach. Intention to treat generally means analyzing participants according to their assigned group, regardless of treatment received, but the precise implementation details are not reported. LOCF carries the last observed value forward when a later value is missing. This can create assumptions about the unobserved outcome, and the registry record does not report sensitivity analyses or other missing-data methods for comparison.

11. Confidence Intervals and Precision

A confidence interval expresses uncertainty around an estimated effect under the statistical method used. It gives a range of effect values that are compatible with the observed data and the model assumptions at the stated confidence level. It is not a guarantee that the true effect lies in the interval, nor does it show the probability that an individual participant will meet the endpoint.

For the primary unadjusted comparison of late locomotor training with early locomotor training, the risk-difference estimate is 0.035 and the 95% confidence interval runs from -0.082 to 0.151. For home exercise compared with early locomotor training, the estimate is 0.012 and the 95% confidence interval runs from -0.108 to 0.133. Both intervals include zero, the value representing no risk difference. Their span across zero means these data do not tightly distinguish no difference from effects in either direction.

The sponsor's logistic-regression confidence intervals also include the null value for an odds ratio, which is 1. The early-training versus home-exercise estimate is 0.831, with a 95% confidence interval from 0.497 to 1.391. The late-training versus home-exercise estimate is 1.192, with a 95% confidence interval from 0.715 to 1.985. These intervals are on the odds-ratio scale and should not be compared numerically with risk-difference intervals as though they measured the same thing.

Precision is affected by the amount of information in the data and by the variability and analysis method. The endpoint group sizes are reported as 139, 143, and 126. The intervals are relatively broad around the primary risk differences, so estimates should not be treated as exact. A non-significant comparison does not demonstrate equivalence; an equivalence conclusion would require an appropriate design, prespecified margin, and analysis, none of which is reported in the registry record.

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 describe hypothetical sample sizes for detecting effects based on fractions of the observed effect. They are participants per arm, not total participants or total events. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is the stated fraction of the observed effect. These are planning illustrations based on the observed result, not the original trial's design justification; the original design assumptions are not reported in the registry record.

The 80% power column gives the number of participants per arm that the planning calculation associates with an 80% chance of detecting the specified effect, if the planning assumptions hold and the assumed effect is real. The 90% power column gives the corresponding per-arm figure for a 90% chance. Power is a property of a planned study under assumptions; it is not a measure of whether the observed trial result is true. This is not observed power.

The displayed rows consider planning for 100%, 75%, and 50% of the observed effect. The smaller the effect one aims to detect, the more participants are needed per arm under otherwise unchanged assumptions. The estimates can rise sharply when planning around a smaller effect, especially when the observed effect used as the starting point is small. These figures are not a recommendation or a claim about the sample size needed for a future study: they depend on the effect assumption, chosen error rates, allocation, and calculation method.

The registry's original sample-size calculation, target power, and assumptions are not reported. The planning figures should therefore be read only as illustrations of how sample size changes under the stated assumptions, rather than as evidence that the LEAPS enrollment was adequate or inadequate for its original aims.

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

Worked calculation for this trial

1. Control proportion p₀ = 0.504; treatment proportion p₁ = 0.538; average p̄ = 0.521.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7065 = 1.3847.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.7061 = 0.5942.
4. n = (1.3847 + 0.5942)² / (0.0349)² = 3,221.7, rounded up to 3,222 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 <- 0.503597122302158                          # control proportion
p1 <- 0.538461538461538                          # 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(243919)
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 = 3,222 (80% power), 4,313 (90% power)
 75% of observed effect: n per arm = 5,733 (80% power), 7,674 (90% power)
 50% of observed effect: n per arm = 12,906 (80% power), 17,277 (90% power)
power.prop.test: 3221.7 
Simulated power at n = 3,222 per arm: 0.796 (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.

14. Analyses Reported by the Sponsor

The registry reports sponsor analyses for the primary endpoint using logistic regression and odds ratios. The listed comparisons are early locomotor training with home exercise and late locomotor training with home exercise. Their estimates are 0.831 and 1.192, with 95% confidence intervals of 0.497 to 1.391 and 0.715 to 1.985, respectively. The reported p-values are 0.481 and 0.501. The confidence intervals include 1, the null value for an odds ratio.

The re-calculations are simple unadjusted comparisons from posted summary statistics. They report risk differences for late training versus early training and home exercise versus early training. Those estimates and intervals answer comparisons on a different scale and use a different reference-group arrangement from the sponsor analyses. They should not be expected to match numerically.

The discrepancy flag is false. The sponsor's analyses are therefore presented alongside the unadjusted re-calculations rather than treated as a conflicting result. The registry record does not report details of covariate adjustment or other model specifications, so no further explanation for differences between effect measures should be assumed. The sponsor analysis is the registry's own reported statistical result; the re-calculations offer a transparent, unadjusted view of comparisons reconstructed from the posted summary statistics.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when several outcomes, time points, or group contrasts are tested. With more tests, the chance of at least one apparently unusual result can increase, even when there is no real group difference. This matters for LEAPS because the registry reports 12 outcome measures and 23 analyses, including primary and secondary outcomes and comparisons across treatment groups. The registry record does not report whether the investigators used a family-wise error control method, another multiplicity procedure, or a prespecified hierarchy of hypotheses.

The primary endpoint is described as an intention-to-treat analysis, and missing data were imputed using the LOCF method. Intention to treat generally seeks to preserve randomized group assignment in the analysis. The registry record does not report the operational details of the analysis population, the amount or pattern of missing endpoint data, or whether all randomized participants were included in each analysis. Those details would help readers assess how closely the implementation followed the intended analysis population.

LOCF uses the last observed value as a substitute for a later missing value. This method can be easy to describe, but it relies on assumptions about the course of outcomes after the last observation. If participants' outcomes would have changed after that point, carrying an earlier value forward may not represent the missing endpoint. The registry record does not report sensitivity analyses using alternative missing-data assumptions, nor does it report the amount of missingness by group. The effect of the imputation approach therefore cannot be assessed from the posted information alone.

The registry record also does not report the trial's full statistical analysis plan, any interim-analysis plan or results, or the original sample-size justification. These omissions do not establish that such plans or analyses were absent; they mean those details are not reported in the registry record. Accordingly, interpretation should distinguish the posted results from unreported design and analysis decisions.

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.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: hospitalization (37.1%), fracture (5.8%), death (4.8%), recurrent stroke (4.3%), limitation in activities of daily living (adl)>48hrs (3.2%).

The adverse-event summary reports participants at risk and participants affected by serious and other adverse events in each group. For serious adverse events, the group counts are 51 of 139 for early locomotor training, 59 of 143 for late locomotor training, and 39 of 126 for home exercise. For other adverse events, the reported counts are 100 of 139, 101 of 143, and 88 of 126, respectively. These are counts of affected participants, not counts of separate event episodes.

The listed serious-event terms include Hospitalization at 37.1%, Fracture at 5.8%, Death at 4.8%, Recurrent Stroke at 4.3%, Limitation in activities of daily living (ADL)>48hrs at 3.2%, and Other at 3.2%. The registry record does not make clear in the posted summary whether these term percentages are calculated across all participants, all serious events, or another denominator. They should be read as the reported term percentages, not as arm-specific rates.

Arm-specific death counts are not reported in the adverse-event data. The presence of Death in the serious-event terms does not supply those missing arm-level counts. These summaries describe reported events; they do not by themselves establish whether an event was caused by an intervention or allow a causal comparison of safety between groups.

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

The primary result describes how often participants in each group met the trial's walking-speed success definition at 12 months. The posted percentages are 50.4% for early locomotor training, 53.8% for late locomotor training, and 51.6% for home exercise. The unadjusted risk-difference intervals include zero, and the sponsor's reported odds-ratio intervals include 1. The results therefore do not provide clear evidence of a group difference on this primary endpoint in the listed analyses.

This does not show that the groups are identical. The confidence intervals allow a range of possible effects, and the registry record does not report an equivalence or non-inferiority design with a prespecified margin. Nor do the findings establish that every treatment is ineffective or that there can be no difference on other outcomes. The endpoint applies a threshold to walking speed, so it does not capture all changes in speed or every dimension of post-stroke function.

The secondary findings include a distinct pattern at 6 months, but they concern a different time point and are among multiple reported outcomes and analyses. Without a reported multiplicity plan, secondary p-values merit more caution than a single prespecified primary test. They should not be used alone to overturn or broaden the primary endpoint conclusion.

The registry record reports an intention-to-treat primary analysis and LOCF imputation, but important details are not reported, including the missing-data distribution and sensitivity analyses. The sponsor's regression model details are also not reported. These uncertainties matter when interpreting the estimates and their precision.

The appropriate statistical conclusion is limited: the posted primary comparisons do not establish a clear difference in the percentage meeting the specified 12-month walking criterion. They do not determine the clinical value of a treatment for an individual, prove equivalence, or answer questions beyond the measured population, endpoint, and follow-up recorded in the trial.

18. Why This Trial Matters Statistically

LEAPS illustrates why the definition of an endpoint matters. The primary outcome is not simply whether walking improved in a general sense; it is whether a participant crossed a specified speed threshold relative to baseline. That classification makes the outcome easy to summarize as a percentage, but it can omit gradations of change and may treat participants near a threshold differently from participants farther from it. Statistical interpretation must stay attached to the actual outcome rule.

The trial also shows why effect estimates and uncertainty should be considered together. The observed group percentages are close, while the confidence intervals for the unadjusted comparisons cover effects in both directions. Reporting only percentages or only p-values would not communicate the full uncertainty. Reporting risk differences, odds ratios, and their intervals also makes clear that analyses using different effect scales and reference groups are not interchangeable.

Another statistical lesson is the distinction between a primary endpoint and a collection of secondary measures. Multiple outcomes can describe a wider range of function, but repeated testing raises the importance of prespecification and multiplicity control. The registry lists many outcomes and analyses but does not report how multiplicity was handled. The timing contrast between the 6-month and 12-month walking classifications also reinforces that time points answer distinct questions and should not be collapsed into one general claim.

Finally, the missing-data approach and the distinction between sponsor analysis and unadjusted re-calculation are consequential. LOCF is reported, but its assumptions and sensitivity are not documented in the registry record. The sponsor's logistic regression provides the registry's own inferential analysis, while unadjusted risk differences provide a different descriptive contrast. Making those distinctions explicit helps readers see what the results estimate and what remains uncertain.

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.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

The registry record leaves several trial-specific details unreported. It does not give the original sample-size justification or its assumptions, so the enrollment cannot be judged against the trial's intended power from this record. The planning illustrations based on observed effects are not a substitute for the original design calculation. Details of random-sequence generation and allocation concealment are also not reported in the registry record.

The primary analysis is identified as intention to treat with LOCF imputation, but the record does not describe the extent or pattern of missing data, the implementation details of the analysis population, or sensitivity analyses under alternative assumptions. Because the primary endpoint is a threshold-based classification, missingness and imputation could affect whether a participant is classified as successful. The available record does not quantify that potential influence.

The registry identifies logistic regression for the sponsor's primary comparisons but does not report model covariates or other specification details. It also does not report whether multiplicity was addressed across the 12 outcome measures and 23 analyses. This is particularly relevant to interpreting the secondary findings and their p-values.

The primary endpoint definition specifies thresholds for baseline speeds below 0.4 m/sec and from 0.4 m/sec up to but below 0.8 m/sec. The registry record does not report the success classification for participants with baseline speed at or above 0.8 m/sec. In addition, the adverse-event summary does not report arm-specific death counts, and its serious-event term percentages have no clearly stated denominator in the posted summary.

These are limitations of what can be assessed from the registry record. They do not establish that unreported methods were not used or that the trial's conduct was deficient; they identify areas where the posted information does not permit a fuller evaluation.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Locomotor Experience Applied Post Stroke Trial — NCT00243919.
• Registry record last updated 2014-07-16; status last verified 2012-12.
• Results first posted 2011-09-22.
• 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

The Locomotor Experience Applied Post Stroke Trial was a completed, randomized, parallel phase 3 study sponsored by Duke University, with 408 participants enrolled. It compared early and late body weight supported treadmill training with a non-specific low intensity Home Exercise Program. Masking is recorded as none.

The primary outcome was the percentage meeting a baseline-dependent walking-speed improvement criterion at 12 months. The posted group percentages were 50.4%, 53.8%, and 51.6% for early training, late training, and home exercise. The unadjusted primary risk-difference intervals include zero, and the sponsor's reported primary odds-ratio intervals include 1.

The registry reports intention-to-treat analysis with LOCF imputation, but does not report the original sample-size justification, detailed model specifications, multiplicity handling, or missing-data sensitivity analyses. The results describe the registered endpoint and comparisons; they do not establish equivalence or resolve questions beyond the posted outcomes and follow-up.