Effectiveness of a Preoperative Pulmonary Rehabilitation Program in Patients Awaiting Lung Resection: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Effectiveness of a Preoperative Pulmonary Rehabilitation Program in Patients Awaiting Lung Resection (NCT01963923), a randomized na study. The primary outcome is Exercise Tolerance.

2. Clinical Question

The clinical question links a preoperative behavioral program to an outcome measured after surgery and hospital discharge. Exercise tolerance was designated the primary endpoint, while health-related quality of life and upper- and lower-body strength were listed as secondary outcomes. The intended question concerns a comparison between groups, not whether an individual participant improved from their own baseline; baseline outcome values are not reported in the registry record.

The target population is described in relation to lung cancer and planned lung resection using video-assisted thoracic surgery. The registry record does not report further details about disease stage, other eligibility criteria, or the characteristics of participants who contributed data to each outcome. This limits how specifically the results can be applied to patient groups beyond the population described in the record. The results are therefore best read as group-level findings for this trial, rather than as a forecast for any particular patient or clinical setting.

3. Trial Design

The registry describes a randomized, single-masked, parallel-group trial. The intervention was a behavioral pulmonary rehabilitation program, and the comparator was clinical routine specified by physicians. The study status is completed, and the recorded enrollment is 40. The listed phase is NA. The sponsor is Universidade da Coruña.

The rehabilitation group description calls for at least 16 sessions. The program is characterized in the registry summary as including endurance and strength training. The control group description says participants completed outcome measures and continued their clinical routine. The registry record does not explain the randomization procedure, the allocation concealment process, or who was masked. Single masking is recorded, but the identity of the masked party or parties is not reported in the registry record.

The primary outcome is exercise tolerance measured three weeks after hospital discharge. Its stated measure is the maximum time sustained during a constant-load cycle endurance test performed at 80% of the maximal workload achieved. The secondary outcomes include health-related quality of life and upper- and lower-body strength, with the stated timeframes after surgery. The registry lists 8 outcome measures, while the posted secondary outcomes include the outcomes. The reported group sizes vary across outcome records, so each result needs to be interpreted using its own recorded analysis sample rather than the enrollment figure.

The start is recorded as 2013-10, primary completion as 2015-07, and overall status as completed. These dates describe the study record, but the registry does not report the trial's original sample-size justification, its statistical analysis plan, or whether interim analyses were planned. It also does not describe the precise schedule of all outcome assessments or the analysis population used. Those omissions matter because design and analysis choices affect how directly a group comparison answers the stated clinical question.

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: During the study period, 40 patients were recruited (20 per arm) but only 12 patients in the control group and 10 patients in the rehabilitation group were included in the analysis due to losses in follow-up

3 Weeks Post-surgery

3 Months Post-surgery

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 Exercise Tolerance, measured over Exercise tolerance 3 weeks after hospital discharge.

The primary endpoint is exercise tolerance, expressed in seconds. It is defined as the maximum time a participant sustained exercise on a constant-load cycle endurance test, with the workload set at 80% of the maximal workload achieved. The stated timeframe is three weeks after hospital discharge. The comparison is the mean result in the rehabilitation group versus the mean result in the control group.

In general, an endurance test provides a standardized way to quantify how long a participant can continue a specified exercise task. A time-based measure can capture performance under a defined test condition, while the mean summarizes the group’s average result. The standard deviation describes the spread of individual results around that average; it is not a measure of uncertainty in the estimated difference between group means.

This endpoint was selected to address the study’s stated question about exercise tolerance after preoperative rehabilitation. The timing is important: the registry describes a postoperative assessment after hospital discharge, not a measurement taken during the rehabilitation program. The record does not report a baseline value for this endpoint, so the posted result is a between-group comparison at follow-up rather than a comparison of change from baseline. The test result should be understood as a measure of performance on this particular exercise test, rather than as a complete measure of physical function or overall recovery.

7. Results Posted in the Registry

• Rehabilitation Group: mean 459.70 versus 341.00 on control; difference 118.70 (95% CI -85.98 to 323.38), standardized effect d = 0.50; z-test p = 0.256.

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.

Health-Related Quality of Life

• 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:
  • Rehabilitation Group: mean 38.00 versus 42.10 on control; difference -4.10 (95% CI -11.24 to 3.04), standardized effect d = -0.48; z-test p = 0.260.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Rehabilitation Group and the control. The interval gives the range of effects that remain compatible with the data.

Upper Body Strength

• 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:
  • Rehabilitation Group: mean 17.00 versus 17.00 on control; difference 0.00 (95% CI -2.89 to 2.89), standardized effect d = 0.00; z-test p = 1.000.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Rehabilitation Group and the control. The interval gives the range of effects that remain compatible with the data.

Lower Body Strength

• 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:
  • Rehabilitation Group: mean 12.20 versus 13.20 on control; difference -1.00 (95% CI -5.79 to 3.79), standardized effect d = -0.18; z-test p = 0.683.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Rehabilitation Group and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover health-related quality of life, upper-body strength, and lower-body strength. Taken together, their group comparisons do not point uniformly in the same direction. The quality-of-life point estimate is lower in the rehabilitation group, the reported upper-body means are equal, and the lower-body point estimate is lower in the rehabilitation group. This mixed pattern does not form a consistent extension of the primary exercise-tolerance estimate.

These measures address related but distinct aspects of postoperative status. A cycle endurance test assesses performance during a specific sustained exercise task, whereas a quality-of-life questionnaire and repetition-based strength measures capture different constructs. Agreement across outcomes might strengthen a coherent interpretation, but disagreement is not necessarily contradictory because the measures are not interchangeable. The registry record does not report correlations among outcomes or a broader model combining them.

The secondary results should carry less weight than the primary result because they are secondary, multiple outcomes were recorded, and the registry does not report a plan for controlling the chance of false-positive findings across comparisons. The comparisons are unadjusted. In general, when many outcomes are examined, some may appear unusual by chance even if there are no underlying differences. Without a prespecified multiplicity strategy, an isolated secondary finding is better treated as exploratory than as confirmatory.

There are also differences in the outcome-specific group sizes, and the registry does not explain why those analysis samples differ. The missing information may reflect availability of measurements or analysis choices, but the reason is not reported in the registry record. The secondary outcomes therefore provide context for the primary result, while their uncertainty, multiplicity, and analysis-population details limit the strength of conclusions that can be drawn from their overall pattern.

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

• Health-Related Quality of Life
• Health-Related Quality of Life
• Upper Body Strength
• Upper Body Strength
• Lower Body Strength
• Lower Body Strength

9. Statistical Interpretation

10. Statistical Methods Explained

The posted continuous outcomes are expressed as group means with standard deviations. A mean is the arithmetic average of the recorded measurements in a group. A standard deviation describes how dispersed those measurements are around the mean. These quantities serve different purposes: the mean locates the group average, whereas the standard deviation describes variation among participants. Neither one alone tells how precisely the difference between group means has been estimated.

The primary comparison is a mean difference, defined in the posted recalculation as the rehabilitation-group mean minus the control-group mean. A positive value therefore indicates a higher mean in the rehabilitation group for this endpoint. The primary estimate is 118.7 seconds. The reported confidence interval and unadjusted p-value are recalculated from the posted summary statistics; the registry record does not report a sponsor analysis for this comparison. The discrepancy indicator is false, so there is no flagged conflict between the posted result and a sponsor estimate.

For a mean difference, the confidence interval describes a range of values compatible with the data and the calculation method, under the model’s assumptions. In general, a wider interval reflects less precision. If the interval contains zero, the data do not rule out no difference under this interval procedure. That does not demonstrate equivalence: an equivalence conclusion requires a defined acceptable range and an analysis designed to assess that range. No equivalence margin is reported in the registry record.

The p-value is another way to summarize the primary comparison under a no-difference reference model. In general, it measures how unusual a result at least as discordant with that model would be if the model and analysis assumptions held. It is not a measure of effect size, clinical importance, or the probability that the result occurred by chance. The primary p-value is unadjusted. The registry record does not report a prespecified significance threshold or a complete analysis plan, although the planning illustration separately states an assumed two-sided significance level of 0.05.

The recalculations use posted group summary statistics and are simple, unadjusted comparisons. They are not substitutes for a participant-level analysis. For example, they cannot incorporate covariate adjustment, repeated measurements, or study-specific modeling unless those elements are available in the posted summaries. The registry record lists no reported analyses, so the analysis methods used by the investigators, including any adjustments or alternative models, are not reported in the registry record. There is no basis for attributing the recalculated comparisons to the sponsor.

Standard errors quantify the sampling uncertainty of a statistic under a statistical model. In general, the standard error of a group mean depends on the group’s variability and the number of observations contributing to that mean. A mean difference combines uncertainty from both groups. When sample sizes are limited and individual results vary considerably, the standard error can be large, which typically produces a wide confidence interval. This helps explain why a point estimate can look notable while remaining uncertain.

Normal approximations are used for the planning illustrations, not as evidence that the trial’s observed outcomes followed a normal distribution. In general, a normal approximation is a convenient method for estimating how many participants might be needed to detect a specified difference under stated assumptions. Its accuracy depends on the design and data conditions. For continuous outcomes, the planning exercise uses the observed effect and pooled variability as inputs, together with equal allocation and the stated significance level. It is an illustration, not the trial’s documented original design calculation.

Over-dispersion is a general concern when outcome variability is greater than a model assumes. If a calculation treats the data as less variable than they really are, it can understate uncertainty and make evidence appear more precise than warranted. For these outcomes, the posted standard deviations provide a direct indication of observed spread, but the registry record does not describe distributional diagnostics or report whether the investigators assessed model fit. The raw values are not posted in the registry record, so those checks cannot be evaluated from the available summaries.

Randomization is intended, in general, to make treatment groups comparable in expectation, including for factors that were not measured. It does not guarantee balance in a small realized sample. The registry identifies the allocation as randomized but does not report the random sequence method, concealment, or whether analyses followed assigned groups. These missing details limit assessment of potential selection and analysis biases. The parallel-group structure means the intervention and control results are compared across groups; the registry does not report a within-person crossover design.

The repeated listing of secondary outcome categories and the absence of reported analyses leave key analytical details unclear. The registry does not state how missing measurements were handled, whether all randomized participants were included in each analysis, how multiple outcomes were handled, or whether any transformations or covariate adjustments were applied. Such information is important for evaluating both the validity and the interpretability of the findings. The reported means and recalculated comparisons remain useful descriptions, but they do not fill those methodological gaps.

11. Confidence Intervals and Precision

The primary mean difference is 118.7 seconds, with a 95% confidence interval from -85.98 to 323.4 seconds. This interval is wide and includes zero. It therefore does not identify a precise direction or magnitude for the group difference. Values below zero correspond to a lower mean test time in the rehabilitation group, while values above zero correspond to a higher mean. The interval spans both possibilities.

In general, a confidence interval is a method for expressing the uncertainty of an estimate. It is not a guarantee that the true value lies within the particular calculated interval, nor does it assign a probability to each value inside it. Its width reflects the amount of information in the data together with the variability and assumptions of the method. A narrow interval would indicate greater precision than a wide interval, but precision alone would not establish clinical importance.

The group standard deviations for the primary endpoint are 264.7 seconds and 216.3 seconds. These indicate substantial variability in observed test times relative to the point estimate. The outcome-specific group sizes are 10 and 12. Together, limited outcome samples and considerable spread contribute to uncertainty in the estimated difference. The registry record does not report a clinically meaningful threshold for this endpoint, so the interval cannot be classified against a stated clinical benchmark.

The secondary confidence intervals also need to be read as estimates with uncertainty, not as definitive rankings of the groups. Their breadth and overlap with zero show why small point estimates should not be overinterpreted. Because the comparisons are unadjusted and the registry does not describe a multiplicity plan, the apparent pattern across outcomes is less conclusive than a prespecified, fully reported analysis would be. The precision evidence supports cautious interpretation rather than a firm claim about the direction or size of effects.

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 required participants per arm for the continuous outcomes; they are not totals of 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 set as the stated fraction of the observed effect. These calculations are planning illustrations based on the observed results, not the trial’s original design assumptions, which are not reported in the registry record.

For the primary endpoint, planning for 100% of the observed effect gives 64 participants per arm for 80% power and 86 participants per arm for 90% power. Planning for 75% of the observed effect gives 114 participants per arm for 80% power and 152 participants per arm for 90% power. Planning for 50% of the observed effect gives 256 participants per arm for 80% power and 342 participants per arm for 90% power. The plotted curve represents the same general relationship between a chosen effect size and the required sample size.

In general, 80% power means that a study designed under the stated assumptions would have an 80% chance of detecting the specified effect at the specified significance level, if that effect and the assumptions were correct. The 90% power column describes a higher planned chance of detecting that same specified effect, under the same assumptions. Greater planned power generally requires more participants. A smaller effect is harder to distinguish from random variation, so planning to detect a smaller fraction of the observed effect requires more participants per arm. These are not observed power estimates; they are prospective illustrations based on assumed effects and methods.

The estimated sample size depends on the observed effect, which is itself uncertain in this trial. A planning exercise that uses a noisy estimate can produce estimates that are too large or too small for a future study. The registry record does not report that these calculations were used to design the completed trial. They should be read as conditional illustrations rather than as evidence about the adequacy of the trial’s original design.

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 = 118.700; pooled standard deviation σ = 239.295.
2. n = 2 × (1.96 + 0.842)² × 239.295² / 118.700² = 63.8, rounded up to 64 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 <- 118.7                      # observed difference in means
sigma <- 239.294525637341                     # 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(1963923)
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 = 64 (80% power), 86 (90% power)
 75% of observed effect: n per arm = 114 (80% power), 152 (90% power)
 50% of observed effect: n per arm = 256 (80% power), 342 (90% power)
power.t.test: 64.8 
Simulated power at n = 64 per arm: 0.796 (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. Multiplicity, Missing Data and Analysis Populations

The registry lists a primary outcome and multiple secondary outcomes, including health-related quality of life and measures of upper- and lower-body strength. When several outcomes are tested, the chance of at least one seemingly notable result can increase. Statistical methods can address this multiplicity, for example by adjusting the decision threshold or by establishing a hierarchy of outcomes in advance. The registry record does not report a multiplicity strategy, a hierarchy for the secondary outcomes, or whether the analyses were prespecified.

The posted comparisons are unadjusted recalculations. That description matters particularly for secondary findings: their p-values should not be interpreted as if each were the only analysis conducted. The registry record lists no reported analyses, so it does not provide the investigators’ detailed model, adjusted estimates, prespecified contrasts, or rationale for selecting analyses. It is not possible to determine whether additional outcomes or analyses were examined but not posted.

Missing-data handling is not reported in the registry record. The outcome-specific group sizes vary, but the record does not explain whether this reflects missing measurements, exclusions, or another reason. It does not state whether any imputation was used or how incomplete follow-up was handled. The treatment of missing observations can affect both the group means and the validity of comparisons, particularly if the availability of an outcome is related to health status or group assignment.

The analysis populations are also not described. The record does not state whether participants were analyzed according to randomized assignment, whether any participants were excluded after randomization, or how adherence to the rehabilitation program was incorporated. The group descriptions specify the assigned routines, but do not establish which participants completed the intended program or contributed to each endpoint. These are not details that can be reconstructed from aggregate means.

For these reasons, the posted results are informative as registry-level summaries but do not support a full audit of the statistical analysis. The original statistical plan, multiplicity decisions, analysis populations, and missing-data procedures are not reported in the registry record. Those omissions should be kept separate from the numerical uncertainty in the confidence intervals: both affect how strongly the findings can be interpreted.

15. 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 20 participants at risk in each group for serious adverse events, with 0 serious events recorded for the rehabilitation group and 0 for the control group. It also lists 20 at risk in each group for other adverse events, with 0 recorded in each group. The serious-event terms list is empty.

These entries mean that no events are recorded in the posted safety fields for the groups and categories described. They do not establish that no events occurred outside the registry’s reporting scope or that the intervention has no safety risks. The registry record does not report the adverse-event collection period, definitions, severity criteria beyond the serious-versus-other categories, or the method used to solicit and verify events. Deaths are not reported in the registry record.

Zero recorded events can be difficult to interpret when the amount of safety information is limited. In general, absence of an event in a dataset does not demonstrate that the underlying event risk is zero. These safety entries should therefore be read as the registry’s posted counts, alongside the stated at-risk group sizes, rather than as a comprehensive safety assessment.

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

The primary result is an estimated difference in average exercise-test time at the registry’s stated postoperative follow-up. The point estimate favors a longer mean time in the rehabilitation group, but its confidence interval is broad and includes differences in either direction. The posted result therefore leaves substantial uncertainty about the size and direction of the group difference.

This finding does not establish clinical effectiveness or a clinically important change. The registry record does not report a threshold for a meaningful difference in seconds, a baseline comparison, or detailed participant-level analyses. The test measures performance on a particular constant-load cycle task; it does not directly summarize every aspect of recovery, physical functioning, or quality of life.

The secondary outcomes add context but do not give a uniform pattern. They involve different measures, have their own uncertainty, and were compared without a reported multiplicity plan. Their results should not be used as a collection of independent confirmations. A more complete interpretation would require the prespecified analysis plan, details of the outcome populations and missing data, and clinical thresholds for judging meaningful change.

Randomization is an important design feature, but it does not remove uncertainty created by limited outcome samples, variable measurements, missing methodological details, or differences between the population studied and other settings. The registry gives the study’s intended population and intervention, but not enough detail to assess how closely the enrolled participants match every group of patients awaiting lung resection.

The results should not be read as advice for an individual or as proof that rehabilitation does or does not produce a particular outcome. They describe the posted group averages and their uncertainty. Further interpretation depends on the clinical relevance of the measured differences, the completeness of the analysis record, and evidence beyond these registry summaries.

17. Why This Trial Matters Statistically

This trial illustrates why an estimated effect should be considered together with its precision. A point estimate alone can suggest a direction, but a broad interval makes clear that the data are also compatible with materially different possibilities. The primary result demonstrates the distinction between the observed group difference and the certainty with which that difference is estimated.

It also highlights the importance of outcome-specific sample sizes. The registry’s overall enrollment is not the same as the number contributing to every posted endpoint. The primary comparison and secondary comparisons have different recorded group sizes, and the reasons for those differences are not reported. Readers need to assess each estimate using the data available for that outcome, rather than treating enrollment as if it were the analysis sample for every measure.

The trial’s combination of a primary endpoint and several secondary outcomes shows why multiplicity and prespecification matter. An outcome pattern can look mixed, and isolated estimates can attract attention, yet interpretation depends on whether the outcomes and analyses were defined in advance and how multiple comparisons were handled. Those details are not reported in the registry record.

Finally, planning estimates based on an observed effect are not a retrospective measure of whether a trial had enough power. They depend on assumptions and on an effect estimate that may be imprecise. The planning illustrations make the relationship between effect size and required sample size visible, while the missing original design assumptions prevent a direct judgment about the trial’s initial sample-size rationale. These distinctions are central to reading clinical trial evidence without overstating what a result can support.

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 outcome sample is limited, and the reported standard deviations show substantial variation in test times. This combination leaves the mean difference imprecise. The registry does not report a clinically meaningful threshold, so the observed estimate and interval cannot be translated into a judgment about clinical importance using a stated benchmark.

The endpoint is measured three weeks after hospital discharge, while the secondary outcomes use postoperative timeframes. The record does not describe baseline values or change scores, so the posted comparisons do not show how each group changed from before surgery. It also does not report details about the timing of discharge, test completion, or whether timing varied among participants.

The registry gives limited information about the enrolled population beyond lung cancer and planned lung resection by video-assisted thoracic surgery. Eligibility criteria, participant characteristics, disease details, and the reasons for missing outcome measurements are not reported in the registry record. The outcome-specific group sizes differ, but the record does not explain the differences. This makes it difficult to assess representativeness, completeness of follow-up, and potential selection in the analyzed data.

Although the trial is recorded as randomized and single-masked, the randomization method, concealment procedures, and identity of the masked party are not reported. The registry also does not specify whether participants were analyzed according to assignment, how adherence was handled, or what statistical models the investigators used. Detailed information on multiplicity, missing data, and the original sample-size rationale is likewise absent.

The posted adverse-event fields contain no recorded events, but the collection period and event definitions are not described. Safety interpretation is therefore limited to those registry entries. Overall, these limitations concern both the precision of the estimates and the amount of design and analysis information available for evaluating them; they do not change the numerical results that are posted.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Effectiveness of a Preoperative Pulmonary Rehabilitation Program in Patients Awaiting Lung Resection — NCT01963923.
• Registry record last updated 2020-05-01; status last verified 2020-04.
• Results first posted 2020-05-01.
• 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

The registry record describes NCT01963923, Effectiveness of a Preoperative Pulmonary Rehabilitation Program in Patients Awaiting Lung Resection. It is recorded as a completed, randomized, single-masked, parallel-group study sponsored by Universidade da Coruña, with enrollment of 40 and phase listed as NA. The recorded start is 2013-10 and primary completion is 2015-07.

The intervention was a preoperative pulmonary rehabilitation program involving endurance and strength training. The control group continued clinical routine specified by physicians. Exercise tolerance, measured as sustained time on a constant-load cycle endurance test, was the primary outcome. Health-related quality of life and upper- and lower-body strength were listed as secondary outcomes.

The primary posted comparison is an unadjusted recalculation from group summary statistics. Its estimate favors a longer mean exercise-test time in the rehabilitation group, but the confidence interval is wide and includes zero. Secondary results show a mixed pattern. The registry record does not report the original sample-size rationale, detailed statistical plan, multiplicity approach, analysis populations, or missing-data procedures.