Study of Ivacaftor in Subjects With Cystic Fibrosis (CF) Who Have the R117H-CF Transmembrane Conductance Regulator (CFTR) Mutation (KONDUCT): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study of Ivacaftor in Subjects With Cystic Fibrosis (CF) Who Have the R117H-CF Transmembrane Conductance Regulator (CFTR) Mutation (KONDUCT) (NCT01614457), a randomized phase 3 study. The primary outcome is Absolute Change From Baseline in Percent Predicted Forced Expiratory Volume in 1 Second (FEV1) Through Week 24.

2. Clinical Question

The study was designed to evaluate efficacy and safety in this mutation-defined cystic fibrosis population. Its central statistical question is about the average between-group difference in change in lung function, as measured by percent predicted FEV1. The registry reports an estimated difference favoring the ivacaftor group, but its confidence interval includes zero. The estimate therefore has appreciable uncertainty, and the primary result does not provide strong statistical evidence of a between-group difference under the reported analysis.

The trial also assessed body mass index, sweat chloride, the respiratory domain of the Cystic Fibrosis Questionnaire-Revised, time to first pulmonary exacerbation, and adverse and serious adverse events. These measures address different aspects of the study: a physiologic lung-function measure, a laboratory measure, a patient-reported measure, a body-size measure, a time-to-event outcome and safety. They do not replace the primary question, and their results should be interpreted in light of the multiple outcomes examined.

3. Trial Design

KONDUCT was a Phase 3 randomized, placebo-controlled, parallel-group study of ivacaftor in subjects with cystic fibrosis who had the R117H-CFTR mutation. The registry lists enrollment as 70 and the study status as completed. The intervention description specifies ivacaftor 150 milligram orally twice daily for 24 weeks; the comparator was a matching placebo tablet on the same schedule.

The registry lists quadruple masking, while the official study title describes the trial as double-blind. Both descriptions indicate masking, but the registry record does not explain the terminology or specify which roles were included in the quadruple-masking designation. Allocation was randomized. The parallel-group model means participants were assigned to one of the study groups rather than being described as crossing between treatments.

The primary endpoint timeframe is baseline to Week 24. The primary analysis population was the Full Analysis Set, defined in the record as all randomized subjects who received at least 1 dose of study drug. The posted primary endpoint groups include 34 subjects in the ivacaftor group and 35 in the placebo group. Analysis counts differ among some secondary outcomes, so the endpoint-specific counts should be used when reading each result rather than assuming one count applies to every analysis.

The registry describes planned assessments of efficacy and safety, but the original sample-size justification, details of the randomization procedure, and the study's original statistical analysis plan are not reported in the registry record. The reported results include a mixed model repeated measures analysis for the primary endpoint and for some continuous secondary endpoints. The record does not give enough detail to reconstruct all modeling choices, such as the full set of model terms or the missing-data assumptions.

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: A total of 70 subjects were randomized, of which 1 subject discontinued the study prior to study drug administration. A total of 69 subjects started treatment.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full Analysis Set (FAS) included all randomized subjects who received at least 1 dose of study drug (ivacaftor or placebo).

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: Full Analysis Set (FAS) included all randomized subjects who received at least 1 dose of study drug (ivacaftor or placebo).

6. Primary Endpoint

The registry lists the primary outcome as Absolute Change From Baseline in Percent Predicted Forced Expiratory Volume in 1 Second (FEV1) Through Week 24, measured over Baseline, Week 24.

The primary endpoint was absolute change from baseline in percent predicted forced expiratory volume in 1 second, or FEV1, through Week 24. FEV1 is the volume of air that can forcibly be blown out in one second after full inspiration. The result is expressed relative to a predicted value, with the registry noting that the calculation used standards selected according to age and gender, as well as height.

Percent predicted FEV1 is used as a standardized measure of lung function: relating the measured volume to a predicted value helps account for characteristics that affect expected lung volume. The endpoint compares change from baseline rather than only the Week 24 measurement, so the analysis concerns how the measure changed during the study in each group and how those changes differed between groups.

The registry reports least-squares means and standard errors for the groups, and a between-group least-squares mean difference from a mixed model repeated measures analysis. Least-squares means are model-based group averages; they need not be identical to simple arithmetic averages. The primary comparison is therefore the estimated difference in change, accompanied by a confidence interval describing its precision. The registry does not report a threshold for a clinically important change in percent predicted FEV1, so statistical interpretation alone cannot establish the clinical importance of a particular estimate.

7. Results Posted in the Registry

• Ivacaftor: mean 2.57 versus 0.46 on control; difference 2.11 (95% CI -1.05 to 5.28), standardized effect d = 0.31; z-test p = 0.191.

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.

Change From Baseline in Body Mass Index (BMI) at Week 24

• 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 errors.
• Result:
  • Ivacaftor: mean 0.49 versus 0.23 on control; difference 0.26 (95% CI -1.56 to 2.09), standardized effect d = 0.07; z-test p = 0.778.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Ivacaftor and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline in Sweat Chloride Through Week 24

• 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 errors.
• Result:
  • Ivacaftor: mean -26.28 versus -2.31 on control; difference -23.97 (95% CI -27.89 to -20.05), standardized effect d = -2.93; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Ivacaftor than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change From Baseline in Cystic Fibrosis Questionnaire-Revised (CFQ-R) Respiratory Domain Score Through Week 24

• 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 errors.
• Result:
  • Ivacaftor: mean 7.56 versus -0.83 on control; difference 8.39 (95% CI 2.34 to 14.44), standardized effect d = 0.66; z-test p = 0.007.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Ivacaftor than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The posted secondary continuous results show a mixed pattern rather than a single direction across every measure. The BMI comparison is imprecise and includes no difference within its confidence interval. The sweat chloride and CFQ-R respiratory-domain comparisons have intervals excluding zero, with estimates in opposite numerical directions because the outcomes use different scales and meanings. These findings should be read as outcome-specific, not combined into a single measure of overall effect.

The primary FEV1 result remains central to the study's stated efficacy question. Secondary outcomes can add context by assessing other aspects of the condition or participant experience, but they do not turn an uncertain primary comparison into a conclusive primary result. Nor does a statistically notable secondary result establish that the trial met its primary objective. The registry does not provide a clinical-importance threshold for these outcomes, limiting interpretation of the size of the reported differences.

Several outcomes were considered, and adjustment for multiplicity is not reported in the registry record. General explanation: if multiple hypotheses are tested, some may appear statistically notable by chance even when there is no true effect for any of them. A prespecified testing hierarchy or multiplicity adjustment can help manage that risk. Without information about such procedures, unadjusted secondary p-values carry less confirmatory weight than a result from a single prespecified primary comparison.

The study description also lists time to first pulmonary exacerbation and adverse and serious adverse events among secondary outcomes. A time-to-event analysis for pulmonary exacerbation is not included among the posted secondary analyses described in the record, so no inference about that endpoint can be drawn from the continuous-outcome results. Safety counts should be interpreted separately from efficacy comparisons.

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

• Change From Baseline in Body Mass Index (BMI) at Week 24
• Change From Baseline in Sweat Chloride Through Week 24
• Change From Baseline in Cystic Fibrosis Questionnaire-Revised (CFQ-R) Respiratory Domain Score Through Week 24
• Time to First Pulmonary Exacerbation
• Number of Subjects With Adverse Events (AEs) and Serious Adverse Events (SAEs)

9. Statistical Interpretation

10. Statistical Methods Explained

The posted outcomes are mostly continuous measures: they can take a range of values, and the analyses summarize changes and compare group averages. The primary endpoint and continuous secondary outcomes are reported as least-squares means with standard errors. A standard error describes the estimated sampling uncertainty of a mean. It is not the same as the spread of individual measurements; it quantifies uncertainty in the estimated mean under the analysis used.

What does the between-group estimate represent?

For a continuous endpoint, the comparison is the estimated mean change in the ivacaftor group minus the estimated mean change in the placebo group. A positive estimate means the estimated change is numerically higher in the ivacaftor group; a negative estimate means it is numerically lower. The interpretation of direction depends on the outcome's scale and what a higher or lower value represents. For example, the registry defines the primary endpoint as change in percent predicted FEV1, while sweat chloride is measured in millimoles per liter. The numerical direction should not be treated as a universal measure of benefit across different scales.

The sponsor's primary analysis is identified as a mixed model repeated measures analysis. General explanation: repeated-measures models can use measurements taken at multiple visits while accounting for the fact that observations from the same participant are related. Such models can estimate average group differences over time and can accommodate some incomplete follow-up under their assumptions. The registry does not report the full model specification, the covariance structure, the exact visit terms, or the assumptions used for missing observations. Those details therefore cannot be evaluated from the registry record.

What does the recalculation add?

The recalculated comparisons are simple, unadjusted comparisons based on the posted summary statistics. For the continuous measures, they estimate a difference between the reported group means and use an approximate pooled standard deviation derived from the reported standard errors and group counts. The calculations do not reproduce the sponsor's repeated-measures model. They are useful as a transparent summary-level check, but they do not replace the sponsor's analysis, which uses the trial's reported model. In this study the discrepancy flag is false, and the recalculated primary result is broadly consistent with the sponsor's reported estimate and inference.

General explanation: a confidence interval gives a range of estimates reasonably compatible with the observed data under the model and its assumptions. A 95% confidence interval is constructed by a method that, over repeated studies under those assumptions, would cover the underlying quantity in 95% of such intervals. It is not a statement that there is a 95% probability that the fixed treatment effect lies in this particular interval. If an interval for a difference includes zero, the data do not exclude no difference at that confidence level. That does not prove no effect, and an interval excluding zero does not by itself establish clinical importance.

Why can over-dispersion matter?

General explanation: over-dispersion occurs when variation in the data is greater than the statistical model expects. If it is ignored, standard errors can be too small and confidence intervals too narrow, making evidence look more precise than it is. The outcomes are continuous means, and the registry does not identify an over-dispersion analysis or a need for one. The concept is relevant as a general modeling concern, but there is no basis in the record to assert that over-dispersion affected these results.

The primary endpoint is reported for the Full Analysis Set, defined as randomized subjects who received at least 1 dose of study drug. The sample counts in the posted continuous outcomes vary, which can reflect analysis-specific availability or rules, but the registry does not report the reasons for those variations. It would be inappropriate to infer why a measurement was unavailable or to assume a particular imputation method.

For the primary recalculation, the unadjusted p-value is 0.191. A p-value describes how unusual results at least as incompatible with a null hypothesis of no difference would be under that null hypothesis and the statistical assumptions. It is not the probability that the null hypothesis is true, nor does it measure the size or importance of an effect. P-values also do not convey precision on their own; the estimate and confidence interval are needed to understand the range of compatible differences.

The secondary continuous outcomes have their own estimates and intervals. General explanation: testing several outcomes creates a multiplicity issue because the chance of at least one apparently notable result can rise when many hypotheses are considered. Adjustments or a prespecified hierarchy can address that issue, but the registry record does not report whether such a procedure was planned or used. The displayed secondary p-values are therefore best interpreted as unadjusted evidence for their individual comparisons, not as definitive confirmation across a family of outcomes.

11. Confidence Intervals and Precision

The primary between-group estimate is 2.111, and its 95% confidence interval ranges from -1.055 to 5.278. The interval crosses zero, so the primary estimate is not statistically distinguishable from zero at the usual 5% level based on this interval. Its width also indicates that the data leave room for meaningfully different possible values of the underlying between-group difference. The registry does not provide a clinical threshold against which to judge those values.

General explanation: a confidence interval communicates both direction and precision. A narrow interval indicates that the estimate is more precise under the analysis assumptions; a wide interval leaves greater uncertainty. When an interval spans zero, it includes values corresponding to differences in either direction and no difference. This does not show that every value in the interval is equally likely, and it does not mean that the true effect has a 95% probability of being inside the observed interval.

The sponsor's repeated-measures analysis gives a similar primary estimate and likewise reports an interval spanning zero. The small differences between the summary-statistic recalculation and the sponsor's model-based interval reflect that they are not identical analyses. For interpretation of the trial, the sponsor's own analysis takes precedence over the simple recalculation.

Precision also varies across secondary outcomes. The reported sweat chloride and CFQ-R intervals exclude zero, while the BMI interval includes zero. Those intervals concern different units and constructs, so their widths should not be compared as though they were on a common scale. Differences in the outcome-specific analysis counts also matter for precision. The record does not report enough detail to attribute varying precision to a particular cause such as missing measurements, variability, or model specification.

Statistical precision is not the same as clinical importance. Even a precise difference could be too small to matter clinically, while an imprecise estimate might include values of substantial interest. The registry does not report a minimally important difference for the primary or secondary outcomes, so the confidence intervals can describe statistical uncertainty but cannot resolve that clinical judgment.

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 the continuous-outcome comparisons, not total events. They are planning illustrations computed from the observed effect, not the trial's original sample-size design. The 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 to the stated fraction of the observed effect: 100%, 75%, or 50%.

The 80% power column gives the number of participants per arm that the illustration estimates would be needed to have an 80% chance of detecting the assumed difference at the specified significance level, if that difference and the planning assumptions were correct. The 90% power column applies the same idea with a higher chance of detection, which generally requires a larger planned sample. These values concern future planning under assumptions; they do not describe the chance that the completed trial found a real effect.

Smaller assumed effects require more participants because they are harder to distinguish from random variation. The observed effect is only an estimate from this trial and may not be a stable forecast of the effect in a future study. Planning around a fraction of that estimate provides a way to examine sensitivity to smaller effects, rather than a guarantee that those effects are true or attainable. The original trial's own sample-size assumptions and justification are not reported in the registry record. These illustrations are not observed power.

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 = 2.111; pooled standard deviation σ = 6.708.
2. n = 2 × (1.96 + 0.842)² × 6.708² / 2.111² = 158.5, rounded up to 159 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 <- 2.1113                      # observed difference in means
sigma <- 6.7083414775044                     # 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(1614457)
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 = 159 (80% power), 213 (90% power)
 75% of observed effect: n per arm = 282 (80% power), 378 (90% power)
 50% of observed effect: n per arm = 634 (80% power), 849 (90% power)
power.t.test: 159.4 
Simulated power at n = 159 per arm: 0.802 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The sponsor reports the primary comparison from a mixed model repeated measures analysis, with a least-squares mean difference and a 95% confidence interval. The sponsor's estimated difference and the summary-statistic recalculation are close, and both confidence intervals include zero. The sponsor's reported p-value also leads to the same broad statistical reading as the unadjusted recalculation: the primary comparison is not statistically significant at the conventional 5% level.

The recalculation uses posted summary statistics and an approximate standard deviation; it does not reproduce the sponsor's repeated-measures model. It is a simple check, not an alternative primary analysis. Because the discrepancy flag is false, there is no material conflict identified between the two presentations. The sponsor's own analysis takes precedence for interpreting the trial's primary result.

For secondary continuous outcomes, the sponsor also reports model-based analyses. Their results are broadly consistent with the recalculated comparisons, but the modeling details and the handling of missing measurements are not fully described in the registry record. The sponsor's reported analysis should be kept distinct from the summary-level calculations, particularly when interpreting confidence intervals and p-values that may differ slightly because the methods are not identical.

15. Multiplicity, Missing Data and Analysis Populations

The study has a stated primary endpoint and multiple secondary outcomes. The registry lists body mass index, sweat chloride, CFQ-R respiratory-domain score, time to first pulmonary exacerbation, and adverse and serious adverse events as secondary measures. The posted analyses include the primary endpoint and continuous analyses for BMI, sweat chloride, and CFQ-R; an analysis of time to first pulmonary exacerbation is not reported among the posted results described in the record.

Multiplicity matters because examining several outcomes can increase the chance of obtaining at least one low p-value by chance. Statistical approaches can control that risk, for example by adjusting significance thresholds or specifying an ordered testing strategy. Whether the study used such an approach, and whether any secondary findings were designated as confirmatory, are not reported in the registry record. The secondary p-values should therefore be understood as unadjusted individual comparisons unless otherwise specified in the record.

The primary analysis population is defined as randomized subjects who received at least 1 dose of study drug. Outcome-specific group counts vary across the posted continuous analyses. The record does not explain the reasons for those variations, describe how missing measurements were handled, or report sensitivity analyses assessing the impact of missing data. It also does not provide enough information to evaluate whether the model's missing-data assumptions were appropriate.

The full statistical analysis plan, the original sample-size justification, and details of interim analyses are not reported in the registry record. It is therefore not possible to determine from the record whether analysis choices were fully prespecified, whether an interim analysis occurred, or how any such analysis would have affected interpretation. These are uncertainties about the available reporting, not evidence that a particular procedure was or was not used.

The endpoint-specific estimates remain informative descriptions of the posted analyses, but conclusions should reflect these reporting limits. In particular, the primary result should be distinguished from the secondary findings, and the latter should not be treated as a family of definitive tests without information about multiplicity control.

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: infective pulmonary exacerbation of cystic fibrosis (17.1%), cellulitis (2.9%), constipation (2.9%).

The registry reports serious adverse events for 4 of 34 subjects in the ivacaftor group and 6 of 35 subjects in the placebo group. It reports other adverse events for 32 of 34 subjects in the ivacaftor group and 35 of 35 subjects in the placebo group. These are counts of subjects with reported events in each group; they are not estimates of a causal treatment effect, and the record does not provide a comparative statistical analysis of these counts.

The most frequent serious-event terms listed are infective pulmonary exacerbation of cystic fibrosis at 17.1%, cellulitis at 2.9%, and constipation at 2.9%. These terms describe events recorded in the registry; they do not by themselves establish that study treatment caused an event. The registry record does not report deaths. It also does not provide enough information in these summary figures to assess event timing, severity beyond the serious classification, exposure-adjusted rates, or the relationship of each event to study drug.

Safety counts are best read descriptively, with attention to the group denominators and the definitions used for adverse and serious adverse events. The figures alone do not show whether differences between groups are statistically reliable.

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

The primary result is an estimate of the between-group difference in change in percent predicted FEV1 through Week 24. Its confidence interval includes zero, and the unadjusted recalculated p-value is 0.191. The result therefore does not provide strong statistical evidence of a difference under the reported primary analysis. It also does not establish that the groups had exactly the same outcome: the interval remains compatible with a range of possible differences.

The posted secondary continuous outcomes do not all point in the same way. Some intervals exclude zero and others do not, but those outcomes have different scales and measure different features. Multiple testing and the absence of a reported adjustment make isolated secondary p-values less conclusive. The registry does not report a clinical-importance threshold for the outcomes, so statistical significance should not be equated with clinical importance.

This interpretation is limited to the trial population and duration described in the record: subjects with cystic fibrosis and the R117H-CFTR mutation, assessed through the stated 24-week treatment period. It does not establish what would occur in people with other mutations, over a different duration, or under a different study design. The record does not provide enough detail about missing-data handling, the full analysis plan, or the original sample-size rationale to resolve all uncertainties about the analysis.

The safety figures are descriptive counts and do not establish whether treatment caused reported events. The registry does not report deaths in the posted safety information. Taken together, the results allow a careful account of the measured outcomes and their statistical precision, but they do not support a broader conclusion that goes beyond the reported population, endpoints, follow-up, and analyses.

18. Why This Trial Matters Statistically

This trial illustrates why an estimated effect, its confidence interval, and the analysis plan all matter. The primary point estimate is positive, yet its interval spans zero. Reading the estimate alone could overstate certainty; reading only whether a p-value crosses a threshold could obscure the range of values still compatible with the data. The interval makes that uncertainty visible.

The comparison also illustrates the difference between a sponsor's model-based analysis and a summary-statistic recalculation. The recalculation is a transparent unadjusted check, while the sponsor's mixed model repeated measures analysis uses a different method. Their broadly similar primary results provide a useful consistency check, but the model-based result remains the principal reported analysis.

The secondary outcomes add statistical complexity. They cover distinct measures, with some reported comparisons excluding zero and others not. Without reported multiplicity procedures, the most notable secondary p-values deserve more caution than a single prespecified primary test. This is an important distinction in clinical research: multiple measures can enrich understanding while also making selective emphasis a risk.

Finally, the planning illustrations show how assumptions about the effect size influence required sample sizes. Planning for smaller effects requires more participants, but calculations based on an observed estimate are not a substitute for the original design rationale. The registry record does not report that rationale, so the illustrations should be treated as prospective planning aids rather than an explanation of how this trial was sized.

19. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

The registry reports enrollment of 70, and the primary endpoint groups include 34 subjects receiving ivacaftor and 35 receiving placebo. The primary confidence interval spans zero and remains compatible with a range of effects, so the estimate is not highly decisive. The registry does not report the original sample-size justification, preventing assessment of the assumptions used to plan the study.

The study concerns a specific population: subjects with cystic fibrosis who had the R117H-CFTR mutation. The record does not establish how the findings would apply to people with other CFTR mutations or other populations. Follow-up for the intervention is described as 24 weeks; longer-term outcomes are not established by this duration.

The available analysis details are incomplete. The registry identifies a mixed model repeated measures method for the primary endpoint, but does not report the full model specification, the missing-data method, sensitivity analyses, or the full statistical analysis plan. Analysis counts vary by endpoint, and reasons for those differences are not reported. The registry also does not report whether multiplicity was addressed.

Some listed secondary outcomes do not have a posted analysis among the results described in the record, including time to first pulmonary exacerbation. The record also does not report a clinical-importance threshold for the primary or secondary outcomes. These limitations restrict interpretation of clinical relevance and of how broadly the posted results can be generalized; they do not, on their own, establish bias or invalidate the reported analyses.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Study of Ivacaftor in Subjects With Cystic Fibrosis (CF) Who Have the R117H-CF Transmembrane Conductance Regulator (CFTR) Mutation (KONDUCT) — NCT01614457.
• Registry record last updated 2015-02-12; status last verified 2015-01.
• Results first posted 2015-02-12.
• 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

KONDUCT was a completed Phase 3 randomized, placebo-controlled, parallel-group study of ivacaftor in subjects with cystic fibrosis who had the R117H-CFTR mutation. Ivacaftor and matching placebo were taken orally twice daily for 24 weeks. The primary endpoint was absolute change from baseline in percent predicted FEV1 through Week 24, analyzed in the Full Analysis Set.

The primary estimate was 2.111, with a 95% confidence interval from -1.055 to 5.278 and an unadjusted recalculated p-value of 0.191. The sponsor's model-based analysis is similar and also has a confidence interval spanning zero. Secondary continuous outcomes show a mixed pattern, and multiplicity adjustment is not reported. The registry provides descriptive adverse-event counts but does not report deaths.

The main interpretive limits are uncertainty in the primary estimate, incomplete reporting of missing-data and multiplicity methods, and the specific population and 24-week duration.