Implementing a Hospital-Based Walking Program (STRIDE): Function QUERI 2.0: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Implementing a Hospital-Based Walking Program (STRIDE): Function QUERI 2.0 (NCT04868656), a randomized na study. The primary outcome is Penetration.

2. Clinical Question

3. Trial Design

NCT04868656 is a completed, randomized, parallel-group study of implementation strategies for spreading STRIDE, a supervised walking program for hospitalized older Veterans. The registry records an enrollment of 35 and describes the study as a type III effectiveness-implementation hybrid design. Its stated overall goal was to implement, evaluate, and sustain STRIDE in 32 additional VA hospitals. The trial compares two forms of implementation support, rather than assigning participants to different walking or medical treatments.

Sites were allocated to Foundational Support or Enhanced Support. The reported primary-outcome counts are 19 for Foundational Support and 16 for Enhanced Support, with outcome data collected at the site level. The study is listed as randomized, with no masking, and with a parallel model. The registry identifies the interventions as implementation strategies. Its description states that Enhanced Support starts with the same activities as Foundational Support; sites that do not meet initial program benchmarks within 6 months receive higher-intensity support for a period of 4-6 months in addition to continuing Foundational Support.

The registry lists the study start as 2021-06-01, primary completion as 2024-01-26, and status as completed. It identifies Early Ambulation as the condition and the VA Office of Research and Development as sponsor. The registry record does not report the original sample-size justification, the detailed randomization procedure, or further allocation details. The number of sites assigned to each strategy is reported in the outcome results, but the broader recruitment and site-selection process is 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

Analysis population for the primary outcome, as defined in the registry: Data collected at the site level

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: Data was collected at the site level and these characteristics were not relevant and not collected.

6. Primary Endpoint

The registry lists the primary outcome as Penetration, measured over 10 months (cumulative).

The primary endpoint is penetration, measured as the percentage of eligible hospitalizations with one or more STRIDE walks at 10 months, cumulatively. It is a continuous site-level measure summarized by its mean and standard deviation. In this setting, penetration describes how widely the program reached eligible hospitalizations at each site; it is an implementation outcome, not a measure of an individual patient's health response to walking.

The registry explains why the denominator is deliberately inclusive: not all eligibility criteria, such as ability to walk at baseline, can be assessed in the Electronic Health Record. Because the denominator may therefore include hospitalizations that would not meet all clinical eligibility criteria, 100% penetration is not considered an appropriate goal. The registry gives an anticipated range from 0% when there is no program activity at the 10-month assessment to 40% as an estimated maximum achievable based on data from current STRIDE sites. These are expectations described in the endpoint definition, not results from this comparison.

Penetration is useful for the implementation question because it captures whether a program is being delivered across eligible hospitalizations, rather than merely whether a hospital has adopted it in principle. It can therefore distinguish implementation reach from the presence of program infrastructure. The outcome does not itself establish why sites reached different levels, whether walking changed patients' health, or whether one support strategy would produce the same pattern in other settings. Those questions require evidence beyond this endpoint.

7. Results Posted in the Registry

• Enhanced Support: mean 2.20 versus 4.30 on control; difference -2.10 (95% CI -4.67 to 0.47), standardized effect d = -0.52; z-test p = 0.110.

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.

Fidelity

• 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:
  • Enhanced Support: mean 40.00 versus 35.00 on control; difference 5.00 (95% CI -3.20 to 13.20), standardized effect d = 0.42; z-test p = 0.232.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Enhanced Support and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes are fidelity and adoption. The registry reports fidelity results, but adoption is listed without an outcome result in the registry record. Across the posted information, the primary penetration comparison has a negative estimated mean difference for Enhanced Support relative to Foundational Support, while the fidelity estimate is positive. This is not a uniform direction across implementation measures. The measures capture different aspects of implementation, so a mixed pattern need not be contradictory: program reach and delivery fidelity are related but distinct constructs.

The secondary results can help frame the primary finding, but they should not be treated as independent confirmation or as a replacement primary endpoint. They are part of a set of outcome comparisons, and the registry record does not report a multiplicity adjustment or a confirmatory hierarchy for them. When several outcomes are tested, the chance of at least one seemingly notable result can increase. General statistical explanation: adjustment procedures or a prespecified testing hierarchy can control how multiple comparisons are interpreted, but the registry record does not say whether such procedures were used beyond the information posted.

The secondary evidence is also limited by what is recorded. Adoption results are not reported in the registry record, and the available description does not provide a full account of how all outcomes were analyzed or how missing values were handled. Fidelity is a secondary implementation measure; its direction can inform hypotheses about the way strategies are delivered, but cannot establish why the primary penetration result has its observed direction. The pattern should therefore be read as descriptive and exploratory unless the sponsor's complete analysis plan supports stronger claims. No such plan is reported in the registry record.

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

• Fidelity
• Adoption

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous: penetration is expressed as a percentage, and the registry summarizes each arm using a mean and standard deviation. The posted arm summaries therefore describe average site-level penetration and the spread of site values around those averages. A mean difference compares the average in one arm with the average in the other. In the reported comparison, the order is Enhanced Support relative to Foundational Support, so a negative estimate indicates a lower mean in Enhanced Support in these data. This direction is descriptive; it does not by itself establish a causal effect or a reliable difference.

What does the mean difference represent?

The recalculated mean difference is -2.1. It is an unadjusted comparison based on the posted summary statistics, rather than a model-based estimate adjusted for other variables. Its meaning is tied to the endpoint's unit: percentage of eligible hospitalizations. It should not be read as a relative percentage change, and it does not mean that every site or every hospitalization had a value that differed by this amount. It compares arm averages, while site-level values may vary within each arm.

The standard deviations describe variability among the observed site-level measurements. They are not confidence intervals for the means and are not measures of uncertainty about the estimated difference. The reported standard deviations are 4.7 for Foundational Support and 3.0 for Enhanced Support. The variation matters because the arm means are estimated from a limited number of sites, and differences between sites contribute to uncertainty in the comparison. The pooled standard deviation used in the recalculation is 4.017; it is a summary quantity for the unadjusted standardized comparison, not a separate observed endpoint.

How should the p-value be read?

The recalculated unadjusted p-value is 0.11. In general, a p-value describes how compatible the observed data are with a specified null model of no difference, under the assumptions of the test. It is not the probability that the null hypothesis is true, nor the probability that a finding is due to chance. A value above a chosen significance threshold does not prove equivalence, and a value below a threshold would not, by itself, establish importance or validity. The registry does not report the significance threshold for the trial's original analysis, so interpretation should not assume that a particular decision rule was used.

The recalculated p-value and interval come from a simple unadjusted calculation using posted summary statistics. The sponsor reports a linear regression analysis with p = 0.15 and a 95% confidence interval from -5.0 to 0.8. The two analyses share the same displayed point estimate, but differ in uncertainty and p-value. Their methods are not identical: a linear regression can incorporate the trial's analysis structure or other terms, whereas the simple recalculation is not adjusted. The registry record does not report enough detail to reconstruct the sponsor model fully. The sponsor's reported result is therefore important for understanding the official trial analysis; the recalculation is a supplementary comparison of the posted summaries.

Why does variation matter?

General statistical explanation: when an outcome varies substantially among sites, an estimated arm difference is less precise unless the study includes enough independent site-level observations to characterize that variability. A small number of sites can leave a wide range of plausible differences even when the arm means are not identical. The reported interval captures this uncertainty in the comparison, rather than the range of individual site values. The endpoint is measured at the site level, so hospitalizations should not be treated as though each were an independently randomized unit based on the description in the registry.

General statistical explanation: over-dispersion occurs when observed variation is greater than a statistical model expects. That can make model-based standard errors and p-values unreliable if the model does not account for the extra variation. The registry does not report an over-dispersion assessment or a model diagnostic, so no such condition can be asserted for these results. More broadly, site-level implementation outcomes may be shaped by site context and support delivery; the registry does not give enough detail to determine how those features were represented in the sponsor's regression.

What is the role of the confidence interval?

A confidence interval gives a range of values compatible with the data under the analysis method and its assumptions. It conveys precision as well as direction. The recalculated interval and the sponsor's 95% interval both include no difference, and both also include effects in either direction. This is why the negative point estimate should not be treated as conclusive evidence of a difference. The intervals do not show the probability that the true effect lies inside them; their interpretation depends on the method and repeated-sampling framework.

These methods do not address every source of uncertainty. The registry record does not report missing-data procedures, the analysis population definition, covariate adjustment details, or whether any interim analyses were conducted. It also does not report the original sample-size calculation or its assumptions. Accordingly, the unadjusted calculations support a transparent reading of the reported summaries, but cannot answer questions about undisclosed design or analysis choices.

11. Confidence Intervals and Precision

Precision is best judged from the confidence interval alongside the point estimate. The recalculated primary mean difference is -2.1, and its interval ranges from -4.674 to 0.474. The interval crosses no difference, so the posted summary statistics are compatible with a negative difference as well as a small difference in the opposite direction. This range is also broad relative to the point estimate, indicating limited precision in the estimated comparison.

The sponsor's regression estimate is also -2.1, with a 95% confidence interval from -5.0 to 0.8. That interval likewise includes no difference and values on both sides of it. The sponsor interval is not identical to the recalculated interval because the sponsor's analysis is a regression, whereas the recalculation is an unadjusted comparison based on summary statistics. The registry does not report sufficient model details to attribute the difference in interval width to a specific adjustment or assumption.

In general, a confidence interval represents the range of effect values compatible with the observed data under a specified method and its assumptions. It is not a range containing most site outcomes, and it does not assign a probability to each possible value. A wider interval means less precision; it does not necessarily mean that the underlying effect is absent. Conversely, a point estimate alone can look specific while concealing substantial uncertainty.

Here, the counts are 19 and 16 in the primary outcome arms, and the endpoint is a site-level measure. That combination calls for care in interpreting apparent differences. The registry does not report a sample-size justification or original design assumptions, so the results cannot be assessed against a documented precision target. The observed estimate is not proof of no difference, and its direction should not be treated as settled. The intervals are the central evidence about how uncertain the comparison remains.

12. Planning a Similar Trial: Sample Size

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

The planning figures are participants per arm for 80% power and participants per arm for 90% power. They are not total event counts: the event-count convention applies only to time-to-event outcomes, and this endpoint is continuous. The planning illustration assumes a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. It uses the observed effect as a starting point, with rows representing planning for 100%, 75%, or 50% of that observed effect. These are planning assumptions for the illustration, not the trial's original design assumptions; the original assumptions are not reported in the registry record.

In general, power is the chance that a study will detect an effect of a specified size under the assumptions of its planning model, if that effect is present. The 80% column gives the estimated number of participants per arm for a design with 80% power under the stated assumptions; the 90% column gives the number per arm for a design with 90% power. A higher target power requires more participants under otherwise unchanged assumptions. The figures are not statements about what happened in this completed study.

The rows that plan for a smaller fraction of the observed effect require more participants, because smaller differences are harder to distinguish from random variation. In general, this makes the assumed effect size a major driver of a sample-size calculation. The observed effect used as a planning reference may itself be uncertain, especially when based on a small study, so such illustrations should not be mistaken for a recommendation about the appropriate design for a future study. These calculations are not observed power.

The registry record does not report the trial's own sample-size justification, its original target for precision or power, or whether the design assumptions included additional considerations. The planning figures therefore provide a hypothetical comparison under the listed assumptions only. They should not be used to infer that the actual trial was planned for a particular power, nor to assess its success by comparing the actual enrollment against an unstated target.

13. How the Sample Size Is Derived

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

Formula

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

Worked calculation for this trial

1. Observed difference Δ = -2.100; pooled standard deviation σ = 4.017.
2. n = 2 × (1.96 + 0.842)² × 4.017² / -2.100² = 57.5, rounded up to 58 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 <- -2.1                      # observed difference in means
sigma <- 4.01746188532013                     # 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(4868656)
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 = 58 (80% power), 77 (90% power)
 75% of observed effect: n per arm = 103 (80% power), 137 (90% power)
 50% of observed effect: n per arm = 230 (80% power), 308 (90% power)
power.t.test: 58.4 
Simulated power at n = 58 per arm: 0.803 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The sponsor reports the primary comparison as a linear regression analysis of final values. The reported mean difference is -2.1, with a 95% confidence interval from -5.0 to 0.8 and p = 0.15. This is the sponsor's own analysis as recorded in the registry and is the main result to use when describing the trial's reported statistical analysis.

The recalculation from the posted arm summaries is an unadjusted comparison. It produces the same displayed mean difference, -2.1, but a different interval, from -4.674 to 0.474, and an unadjusted p-value of 0.11. The numerical difference in uncertainty measures is not, by itself, evidence of an error. A regression analysis may use features not represented in a simple summary-statistic calculation, but the registry record does not report enough model detail to identify the specific reason for the difference.

Both analyses point in the same direction for the estimated mean difference, and both intervals include no difference. The recalculation is useful as a transparent check on the arm summaries, but it is not a substitute for the sponsor's analysis. The registry does not flag a discrepancy between the posted result and recalculation. Neither p-value should be interpreted as the probability that either strategy is superior, and neither interval establishes equivalence.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies a primary outcome and lists fidelity and adoption as secondary outcomes. It does not report a multiplicity procedure, a hierarchy for testing secondary outcomes, or whether the statistical analysis plan designated confirmatory and exploratory comparisons. This matters because evaluating multiple outcomes can increase the likelihood of observing at least one apparently unusual result even when there are no underlying effects. Without a stated plan, secondary p-values, where available, should not be treated as if they carry the same confirmatory weight as a single prespecified primary comparison.

The registry gives a result for fidelity, but adoption results are not reported in the registry record. It does not state how many outcome measures were assessed beyond the posted count, how all comparisons were handled, or whether unreported outcomes were collected. The absence of a reported value does not establish that the outcome was not measured; it means the registry record does not provide a result for it.

Missing-data methods are not reported in the registry record. There is no description of how missing site measurements, incomplete outcome data, or sites that did not reach program benchmarks were handled in the analysis. The record also does not define an analysis population, such as an intention-to-treat or per-protocol population, or say whether all randomized sites were included in each outcome analysis. The reported counts are 19 for Foundational Support and 16 for Enhanced Support, but those counts alone do not establish the missing-data approach.

The record does not report interim analyses, stopping rules, or the original statistical analysis plan. It also does not report details of the regression model, covariates, or assumptions used for the sponsor's analysis. These omissions limit assessment of the full analysis process, but they do not invalidate the results that are posted. They mean that interpretation should remain focused on the registry's reported estimates and their uncertainty, without assuming procedures that are not documented.

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

The posted primary results describe the observed comparison of two implementation support strategies among the sites represented in this study. Mean penetration was lower in the Enhanced Support arm than in the Foundational Support arm, with an estimated mean difference of -2.1. The sponsor's interval and the recalculated interval both include no difference, so the result does not provide a clear statistical distinction between the strategies. The uncertainty also allows values in the opposite direction; the point estimate alone is not a definitive account of the evidence.

This result does not show that the strategies are equivalent. Demonstrating equivalence requires an appropriate design, a prespecified margin, and an analysis suited to that question; those details are not reported in the registry record. A non-significant comparison cannot be interpreted as proof that the two approaches have the same effect. Nor does the result establish that either strategy is ineffective. The study compares implementation support and measures program reach; it is not a direct comparison of clinical outcomes for individual patients.

The endpoint's denominator is inclusive because some eligibility criteria cannot be assessed in the Electronic Health Record. The registry explicitly says that 100% penetration is not an appropriate goal and describes the anticipated range as 0% to 40%. That context is important when interpreting the absolute outcome values: they should not be judged against universal reach as though every hospitalization in the denominator were known to be eligible for walking.

The trial's results are based on 35 enrolled and reported site-level arm counts of 19 and 16. The registry's goal concerns spread to 32 additional VA hospitals, but the registry result should not be generalized automatically to all hospitals, older Veterans, or other health systems. The registry does not describe enough about site selection, analysis populations, missing values, or model details to assess how these factors may shape generalizability. The findings are best understood as an uncertain comparison of implementation outcomes in the reported study, not as a clinical recommendation or a guarantee of future performance.

17. Why This Trial Matters Statistically

This study is statistically interesting because the unit of interest is the hospital site, while the program outcome is expressed through eligible hospitalizations. That distinction affects how results should be interpreted: the primary comparison is between site-level implementation outcomes, not a randomized comparison of individual patient walking outcomes. Treating many hospitalizations as independent observations would not reflect the stated site-level data structure unless an analysis explicitly accounted for clustering; the registry does not provide full details about such modeling.

The endpoint also illustrates that implementation reach depends on how eligibility is measured. The registry acknowledges that electronic records cannot assess every eligibility criterion and cautions that 100% penetration is not an appropriate target. This makes the definition of the denominator integral to the statistical meaning of the result. A percentage can appear straightforward while remaining dependent on the operational definition of eligibility and the quality of routine records.

The randomized comparison is directed at implementation strategy, including an enhanced pathway triggered by failure to meet initial benchmarks. This means the strategy is not simply a fixed dose of support applied identically to every site; the registry describes additional support for a subset meeting a stated condition. The reported comparison is therefore about assignment to the strategy as described, rather than a direct estimate of the effect of higher-intensity support among only sites that received it.

Finally, the primary estimate is accompanied by intervals that communicate considerable uncertainty. The example underscores why the mean difference, confidence interval, and analysis method should be read together. The registry record's limited reporting of design assumptions and analysis details also highlights the value of transparent reporting for interpreting implementation trials.

18. 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 a modest number of site-level observations: 19 in Foundational Support and 16 in Enhanced Support. That limits precision, as reflected in the interval around the mean difference. The registry record does not report an original sample-size justification, so it is not possible to determine whether the study was planned to estimate a particular difference with a particular precision.

The endpoint uses an inclusive denominator because not all eligibility criteria can be assessed in the Electronic Health Record. This measurement limitation is recognized in the registry and affects the interpretation of penetration. The reported percentage may include hospitalizations that would not meet all eligibility criteria, and the registry states that 100% is not an appropriate goal. The record does not report how site-level eligibility denominators were validated or whether measurement differed across sites.

The registry gives limited information about implementation delivery. It identifies the core strategy structure and the condition for additional Enhanced Support, but does not report detailed adherence to each strategy component, the number of sites that received higher-intensity support, or the timing and implementation of that support at each site. Those details would help distinguish the effect of assignment to the strategy from variation in strategy delivery.

Further limitations are reporting gaps rather than established flaws: missing-data procedures, analysis-population definitions, the full regression specification, multiplicity handling, and the original sample-size assumptions are not reported in the registry record. Adoption is named as a secondary outcome, but its results are not reported in the registry record. These gaps prevent a full audit of the statistical analysis and constrain interpretation of generalizability. The record also does not report enough about site selection to establish how well the results represent other hospitals.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Implementing a Hospital-Based Walking Program (STRIDE): Function QUERI 2.0 — NCT04868656.
• Registry record last updated 2025-05-01; status last verified 2025-04.
• Results first posted 2025-05-01.
• 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.

22. Record Summary

NCT04868656 is a completed randomized parallel-group study of Foundational Support versus Enhanced Support for implementing STRIDE, a supervised walking program for hospitalized older Veterans. The registry reports enrollment of 35 and site-level primary outcome counts of 19 and 16. The primary endpoint is cumulative penetration at 10 months, defined as the percentage of eligible hospitalizations with one or more STRIDE walks.

The sponsor's linear regression analysis reports a mean difference of -2.1, with a 95% confidence interval from -5.0 to 0.8 and p = 0.15. An unadjusted recalculation from the arm summaries gives the same point estimate, with an interval from -4.674 to 0.474 and p = 0.11. Both intervals include no difference. Fidelity is listed and has posted results; adoption is listed but its results are not reported in the registry record. The registry does not report the original sample-size justification, missing-data methods, or full analysis details.