Study of the Effect of Ivacaftor on Lung Clearance Index in Subjects With Cystic Fibrosis and the G551D Mutation: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study of the Effect of Ivacaftor on Lung Clearance Index in Subjects With Cystic Fibrosis and the G551D Mutation (NCT01262352), a randomized phase 2 study. The primary outcome is Absolute Change From Baseline in Lung Clearance Index (LCI).

2. Clinical Question

The central statistical question concerns a continuous measure of ventilation inhomogeneity, rather than a clinical event count or a time-to-event outcome. The study record describes a randomized crossover comparison: participants were assigned to treatment sequences in which ivacaftor and placebo were administered in different periods. That design makes the contrast between treatment conditions the focus, while the specific details of how the analysis handled period, sequence, or within-participant correlation are not reported in the registry record.

The posted primary outcome is absolute change from baseline in lung clearance index (LCI), measured through Day 29. Secondary outcomes include change in percent predicted FEV1, sweat chloride, and the respiratory domain of the CF Questionnaire-Revised. These measures address different aspects of the study outcomes; they should not be treated as interchangeable or as multiple ways of measuring the same quantity.

3. Trial Design

The registry record identifies this as a Phase 2 randomized, quadruple-masked, placebo-controlled crossover study. The official title describes it as double-blind. The study enrolled 21 participants and is marked completed. The registry lists cystic fibrosis as the condition and Vertex Pharmaceuticals Incorporated as the sponsor. The recorded start was 2011-01 and primary completion was 2011-11.

In a crossover design, participants receive more than one study condition in separate treatment periods, with the assigned order represented by treatment sequences. The record lists two sequences. Treatment Sequence 1 received ivacaftor in Treatment Period 1 and placebo in Treatment Period 2. Treatment Sequence 2 received placebo in Treatment Period 1 and ivacaftor in Treatment Sequence 2, as worded in the registry record. The record does not give further details about period duration, a washout interval, or the sequence-generation procedure.

The primary outcome timeframe is baseline through Day 29. The primary analysis population is described as all randomized subjects who received at least 1 dose of placebo or ivacaftor and had available assessments during that timeframe. Posted arm counts differ by outcome: the primary LCI estimates use 18 participants for placebo and 17 for ivacaftor, while other outcomes have their own analysis counts. The registry record does not explain each difference in available counts.

Randomization and masking are features of the design, but their presence does not by itself establish how allocation was implemented or whether masking remained intact. Specific procedures for either are not reported in the registry record. The detailed protocol, treatment-period schedule, and original sample-size justification are also not reported in the registry record. These omissions limit how fully the design and its intended analysis can be reconstructed from the posted information alone.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Before assignment: A total of 21 subjects were randomized; 20 subjects received at least 1 dose of the study drug.

Period 1

Reasons for not completing this period:

Washout

Reasons for not completing this period:

Period 2

Analysis population for the primary outcome, as defined in the registry: All randomized subjects who received at least 1 dose of study drug (placebo or ivacaftor) and had available assessments during the time frame.

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 Absolute Change From Baseline in Lung Clearance Index (LCI), measured over Baseline through Day 29.

The primary endpoint is absolute change from baseline in lung clearance index (LCI), expressed as a ratio, from baseline through Day 29. The registry describes LCI as a measure of ventilation inhomogeneity derived from a multiple-breath washout test. It is calculated from the number of lung volume turnovers required to reduce end-tidal SF6 concentration to 1/40th of its starting value. Lung volume turnovers are defined in the record through cumulative expired volume divided by functional residual capacity.

As a continuous measure, LCI can reflect the degree of unevenness in ventilation rather than recording only whether a participant experienced a particular event. The posted outcome is the change from baseline, so the reported arm estimates describe average movement relative to baseline over the stated timeframe. The placebo least-squares mean was 0.77, and the ivacaftor least-squares mean was -1.3. The registry analysis reports a mean difference in final values between the groups.

General statistical explanation: continuous physiological measures can provide a quantitative way to compare groups, but their interpretation depends on how the measurement is collected and analyzed. An average change does not describe the full range of individual participant responses. Nor does the numerical value alone establish the clinical importance of a difference. The registry record does not state a threshold for a clinically meaningful LCI change, so the magnitude should be read as a statistical contrast in the reported measure rather than as a stand-alone judgment about clinical importance.

7. Results Posted in the Registry

• Ivacaftor: mean -1.30 versus 0.77 on control; difference -2.07 (95% CI -2.89 to -1.25), standardized effect d = -1.67; z-test p = <0.001.

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.

Absolute Change From Baseline in Percent Predicted FEV1

• 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 7.00 versus 0.00 on control; difference 7.00 (95% CI 1.60 to 12.40), standardized effect d = 0.84; z-test p = 0.011.
• 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.

Change From Baseline in Sweat Chloride

• 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 -45.74 versus 0.11 on control; difference -45.85 (95% CI -52.77 to -38.93), standardized effect d = -4.48; 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 CF Questionnaire-Revised (CFQ-R) Score (Respiratory Domain Score, Pooled)

• 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 5.32 versus 1.33 on control; difference 3.99 (95% CI -4.65 to 12.63), standardized effect d = 0.30; z-test p = 0.365.
• 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.

Across the three posted secondary outcomes, the pattern is not uniform. The point estimates differ in direction and scale, and their confidence intervals differ in how precisely they locate the comparisons. This makes the secondary outcomes complementary rather than interchangeable evidence. Each measures a different aspect of the study record, and the results should be interpreted on their own outcome scales.

In broad terms, the secondary estimates do not all provide the same degree of statistical separation between the treatment conditions. The FEV1 and sweat chloride comparisons have intervals that exclude zero in the posted analyses, whereas the CFQ-R respiratory-domain interval includes zero and is comparatively broad. The primary LCI finding is therefore not replicated in an identical form across all secondary outcomes; rather, the secondary results describe a mixed pattern across distinct measures.

These comparisons carry less weight than a single prespecified primary outcome when several outcomes are examined and no multiplicity plan is reported. General statistical explanation: testing multiple outcomes creates more opportunities for apparently notable findings to occur by chance. Adjustments or a hierarchy of hypotheses can address this issue, but the registry record does not report whether either approach was used for the secondary outcomes. Their unadjusted results should consequently be treated as supportive or exploratory descriptions rather than as a set of independent confirmatory conclusions.

The record lists the secondary outcomes and their analyses but does not state the order in which they were prioritized, whether they were powered independently, or whether an adjustment was applied. Their estimates can inform the overall statistical picture, but they do not by themselves establish a consistent effect across measures. The measures, intervals, analysis counts, and missing-data context all matter when reading the broader pattern.

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

• Absolute Change From Baseline in Percent Predicted FEV1
• Change From Baseline in Sweat Chloride
• Change From Baseline in CF Questionnaire-Revised (CFQ-R) Score (Respiratory Domain Score, Pooled)

9. Statistical Interpretation

10. Statistical Methods Explained

The registry reports arm-level least-squares means with standard errors for the continuous outcomes and a mixed models analysis for the primary and secondary comparisons. It also posts confidence intervals and p-values for the sponsor analyses. The additional unadjusted re-calculations use posted group summary statistics and are not substitutes for the sponsor's model-based results. They offer a simple way to inspect the direction and approximate precision of a contrast.

What does a mean difference represent?

A mean difference expresses a contrast between two group estimates on the outcome's original scale. For LCI, the posted placebo mean change is 0.77 and the ivacaftor mean change is -1.3; the unadjusted re-calculated contrast is -2.07. The negative sign indicates that the ivacaftor estimate is lower than the placebo estimate. It does not, on its own, explain why the values differ or establish clinical importance. The outcome's unit and measurement definition remain important to interpretation.

The registry's arm values are least-squares means, which are model-based estimates. The sponsor analysis is described as a Mixed Models Analysis of Mean Difference (Final Values). The registry record does not specify the model formula, covariates, covariance structure, or the precise handling of baseline measurements. It is therefore not possible to reproduce or fully evaluate the model from the summary output alone.

Why is the crossover structure relevant?

General statistical explanation: a crossover study observes participants under more than one treatment condition, so measurements from the same participant may be related. Analysis methods can account for this dependence and for treatment period or sequence. Treating measurements as if every observation came from an unrelated participant may not represent the design. The registry labels the sponsor method as mixed models, but does not report enough detail to determine exactly how within-participant dependence, period, or sequence entered that model.

The simple re-calculations are explicitly approximate and based on posted summary statistics. The listed pooled standard deviations are marked as approximations derived from standard errors. They do not encode the full crossover structure. Consequently, their confidence intervals and unadjusted p-values are useful as rough independent-group comparisons of the summaries, not as a second implementation of the trial's mixed model.

How should a p-value be read?

General statistical explanation: a p-value describes how compatible the observed data are with a specified null model, under the assumptions used for the analysis. A small p-value is not the probability that the null hypothesis is true, nor does it measure the size or clinical importance of an effect. It should be interpreted with the estimate, its confidence interval, the design, and the analysis assumptions. The registry posts p-values for the sponsor analyses, and the re-calculation reports unadjusted p-values; the record does not report a multiplicity adjustment for the secondary outcomes.

For the primary sponsor analysis, the posted estimate is -2.069 and its 95% confidence interval is -2.98 to -1.15. The unadjusted re-calculation gives -2.07 and an interval from -2.893 to -1.247. These methods yield closely aligned estimates and intervals, but the sponsor's mixed model remains the analysis reported by the registry. The small distinction in method matters: an approximate re-calculation should not be described as a reproduction of an adjusted or design-specific model.

What does over-dispersion mean in general?

General statistical explanation: over-dispersion occurs when observed variation is greater than a model's assumptions allow. It is especially relevant for outcomes analyzed as counts or proportions, where underestimated variation can make uncertainty appear too small. The posted primary endpoint is continuous and the registry presents standard errors, not a count model. The record does not report an over-dispersion assessment, so there is no basis to say that one was or was not needed. The general concept is useful when evaluating statistical assumptions, but it should not be mistaken for a reported feature of this analysis.

Likewise, a standard error describes uncertainty around an estimated mean under the analysis used; it is not the spread of individual participant values. The LCI standard errors are 0.291 for placebo and 0.303 for ivacaftor. Those values help describe the precision of the arm-level mean estimates, but do not reveal the full distribution of individual changes. The registry does not post individual participant data or a distributional summary sufficient to assess departures from a model's assumptions.

The record does not report interim analyses, a prespecified detailed statistical analysis plan, or the trial's original sample-size justification. The posted planning illustrations are calculated from observed effects under stated assumptions and should be distinguished from the design rationale used before the trial. That distinction prevents a retrospective calculation from being mistaken for a prospective feature of the study.

11. Confidence Intervals and Precision

The sponsor's primary estimate is a mean difference of -2.069, with a 95% confidence interval from -2.98 to -1.15. The interval lies on the negative side of zero and gives a range of values compatible with the model-based estimate and its assumptions. The unadjusted re-calculation is -2.07, with an interval from -2.893 to -1.247. These intervals are close, although they arise from different approaches and the simple re-calculation does not reproduce the mixed model.

General statistical explanation: a confidence interval conveys uncertainty about an estimated contrast. A narrower interval indicates greater statistical precision under the method's assumptions; a wider interval leaves more possible values compatible with the data. The interval is not a range containing every individual participant's response, and it does not assign a probability to a particular fixed value after the analysis has been performed.

The primary result is based on modest outcome-specific counts: 18 participants in the placebo arm and 17 in the ivacaftor arm. Small samples can make estimates sensitive to individual observations and model assumptions. The standard errors for the two arm-level means are 0.291 and 0.303, respectively. Those standard errors describe uncertainty in the estimated means, not the variability of participant-level changes.

Precision should also be considered in relation to the crossover design. A model that accounts for repeated measurements and treatment periods can use the design differently from a simple independent-group calculation. The registry labels the reported analysis as mixed models but does not provide sufficient details to assess that specification fully. Thus, the sponsor's interval is the principal reported model-based uncertainty measure, while the re-calculated interval is an approximate complementary check.

The confidence interval addresses statistical uncertainty, not whether the estimated difference matters to participants or clinicians. A threshold for a clinically important change in LCI is not reported in the registry record. It is therefore possible to describe the estimate and its precision without asserting a clinical interpretation that the record does not establish.

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 figures are planning illustrations based on the observed effect, not the trial's original enrollment plan. For these continuous outcomes, the figures refer to participants per arm, not total events. The registry's stated illustration assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. Each planning row uses the stated fraction of the observed effect as the effect to detect.

The 80% power column gives the illustrated number of participants per arm for a design that would have an 80% probability of detecting the assumed effect under those planning assumptions. The 90% power column gives the corresponding number per arm for a 90% probability. These are planning concepts: power is a property of a proposed design under specified assumptions, not a measure of whether the completed study found a result.

Rows that plan for 75% or 50% of the observed effect use smaller target effects than the row based on 100% of the observed effect. Smaller effects are generally harder to distinguish from random variation, so they require more participants in these illustrations. The resulting figures vary substantially by outcome because the observed estimates and their variability differ. They should not be read as recommendations or as evidence that the completed study had a particular power.

This is not observed power. The trial's original sample-size justification and design assumptions are not reported in the registry record. The illustrations are retrospective and depend on the observed effect, so they should be read as conditional planning scenarios rather than as an explanation for why the study enrolled 21 participants.

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 = -2.070; pooled standard deviation σ = 1.242.
2. n = 2 × (1.96 + 0.842)² × 1.242² / -2.070² = 5.6, rounded up to 6 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 <- -2.07                      # observed difference in means
sigma <- 1.24175381837728                     # 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(1262352)
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 = 6 (80% power), 8 (90% power)
 75% of observed effect: n per arm = 11 (80% power), 14 (90% power)
 50% of observed effect: n per arm = 23 (80% power), 31 (90% power)
power.t.test: 6.8 
Simulated power at n = 6 per arm: 0.741 (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's reported primary mixed models analysis estimates a mean difference in final values of -2.069, with a 95% confidence interval from -2.98 to -1.15. Its reported p-value is < 0.001. The simple unadjusted re-calculation from the posted summaries gives a mean difference of -2.07, a confidence interval from -2.893 to -1.247, and p < 0.001. The estimates are very close in direction and magnitude, and both intervals exclude zero.

The re-calculation is a simple comparison of posted summary statistics. It does not reproduce the mixed models method and does not incorporate any model features that may account for the crossover design. The sponsor's reported analysis is therefore the relevant model-based result in the registry record. The re-calculation is best used as a transparent check of the summary contrast rather than as a replacement for that analysis.

The registry does not report enough detail to reconstruct the sponsor model, including its full specification and handling of period and sequence. Close agreement between the two estimates is informative about the reported contrast, but it does not resolve the unreported modeling details or establish that all assumptions were met. No discrepancy flag is recorded for this comparison.

15. Multiplicity, Missing Data and Analysis Populations

The registry record lists one primary outcome and three secondary outcomes, with analyses posted for each. It does not report a multiplicity strategy, such as a correction across secondary tests, a prespecified hierarchy, or another method for controlling the chance of false-positive findings when several comparisons are examined. As a result, the posted secondary p-values should be read as unadjusted unless the registry explicitly identifies otherwise. The record does not establish whether a multiplicity plan existed outside the registry entry.

The record also does not report a complete statistical analysis plan. Details such as the model formula, covariate adjustment, treatment of period and sequence, missing-data assumptions, and any sensitivity analyses are not reported in the registry record. These omissions make it difficult to determine whether the posted analysis followed a prespecified plan or how alternative reasonable modeling choices might affect the estimates.

The primary analysis population is described as randomized participants who received at least 1 dose and had available assessments during the timeframe. This is a defined analysis population, but the registry does not provide participant-level missingness, reasons for missing outcomes, or an account of how missing values were handled in the mixed model. The primary analysis counts are 18 for placebo and 17 for ivacaftor, while outcome-specific counts vary. The registry does not explain the reasons for these differences.

In general, missing outcome data can affect an estimate if availability is related to treatment or to the outcome being measured. That is a general concern, not a finding about this study. Without details on missingness patterns and analysis assumptions, the direction or size of any potential effect cannot be determined from the registry record.

Interim analyses are not reported in the registry record. Nor is a detailed account of protocol deviations or analysis-set exclusions. These absences do not show that such procedures were or were not conducted; they mean that the public registry information is insufficient to evaluate them. The results can be described as posted, while the unreported procedures remain an important qualification for statistical interpretation.

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: pseudomonas infection (5.6%), cystic fibrosis lung (5.6%), distal ileal obstruction syndrome (5.6%), bronchopulmonary aspergillosis allergic (5.3%).

The registry lists serious adverse events among 19 participants at risk in the placebo group, with 1 affected, and among 18 participants at risk in the ivacaftor group, with 2 affected. These are counts from the safety record, not the primary efficacy analysis counts. The record also lists other adverse events for 19 placebo participants at risk, with 15 affected, and 18 ivacaftor participants at risk, with 13 affected.

The listed serious-event terms include Pseudomonas infection, Cystic fibrosis lung, Distal ileal obstruction syndrome, and Bronchopulmonary aspergillosis allergic, each with the posted percentages of 5.6%, 5.6%, 5.6%, and 5.3%, respectively. The registry record does not provide further context in these figures about timing, duration, severity beyond the serious-event classification, or whether an event was considered related to study drug. Deaths are not reported in the registry record.

These counts are descriptive and should not be interpreted as a comparative safety estimate by themselves. The numbers at risk differ between groups, the study is small, and the registry summary does not supply the details needed to assess event attribution or uncertainty. The figures describe what is posted in the record; they do not establish causation.

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

The posted primary analysis describes a lower mean change in LCI for the ivacaftor condition than for placebo over the stated timeframe. The sponsor's mixed models estimate is -2.069, with a 95% confidence interval from -2.98 to -1.15. The simple unadjusted re-calculation is close to that estimate. These results describe a statistical contrast in a continuous physiological measure for the analyzed participants.

They do not, on their own, establish the clinical importance of the contrast. The registry does not report a threshold for a clinically meaningful LCI change, nor does a group average show the range of individual participant outcomes. The outcome definition explains how LCI is measured, but a numerical change should not be translated into a broader clinical conclusion without an appropriate interpretive benchmark.

The study enrolled 21 participants, and the primary outcome estimates use 18 participants for placebo and 17 for ivacaftor. This small set of outcome-specific observations means that the estimates and intervals should be considered in light of limited information and the analysis assumptions. The crossover structure is relevant to interpretation, but detailed model handling of period, sequence, and repeated measurements is not reported in the registry record.

The secondary outcomes add information across different measures, but they do not all show the same degree of precision or statistical separation. The registry does not report a multiplicity strategy, so secondary findings should not be treated as independent confirmatory evidence. Safety figures are likewise descriptive counts and do not establish that an event was caused by a treatment.

Overall, the record documents the design, outcome definitions, and posted statistical results, but leaves several protocol and analysis details unreported. The estimates can be read as findings from this small Phase 2 crossover study; they should not be expanded into claims beyond the measured outcomes, analyzed population, and methods described in the registry.

18. Why This Trial Matters Statistically

This study illustrates why the design and the analysis must be read together. A crossover trial exposes participants to both study conditions in separate periods, so a statistical comparison may need to account for within-participant dependence as well as treatment period and sequence. The registry labels the reported analysis as mixed models, but does not give enough detail to evaluate how these design features were handled.

It also shows why an estimate and its uncertainty are more informative than a p-value alone. The primary contrast is accompanied by a confidence interval, allowing readers to assess both direction and precision. The close alignment between the sponsor's reported estimate and the approximate re-calculation offers a useful consistency check, while the differing methods remind readers that summary-statistic calculations do not replace design-aware modeling.

The posted secondary outcomes illustrate a separate issue: several measures can be examined, but their results do not automatically have equal confirmatory status. Without a reported multiplicity strategy or hierarchy, readers should distinguish the primary analysis from the secondary comparisons and avoid treating each unadjusted result as definitive in isolation.

Finally, the registry record separates the existence of a result from the completeness of its statistical account. It reports outcome estimates, intervals, and participant counts, but does not report the original sample-size justification, a detailed analysis plan, or several missing-data and model specifications. This is an important statistical lesson: transparent interpretation depends not only on the numerical result, but also on knowing which assumptions and procedures produced it.

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.

Several trial-specific limitations follow from the information in the registry. The study enrolled 21 participants, and the primary LCI estimates use 18 participants in the placebo group and 17 in the ivacaftor group. Outcome-specific counts differ, but the registry does not explain the reasons for those differences or describe missingness patterns. The size and availability of the analyzed samples limit how broadly the estimates can be interpreted.

The crossover design makes period, sequence, and within-participant dependence relevant to the analysis. Although the sponsor method is labeled Mixed Models Analysis, the registry does not report the model specification or its treatment of these features. A simple re-calculation from summary statistics cannot resolve this limitation, because it is not a reconstruction of the sponsor's model.

The record does not report the original sample-size justification, a detailed statistical analysis plan, interim analyses, or a multiplicity strategy. It also does not state a clinically meaningful threshold for LCI change. These gaps constrain assessment of the planned role of each outcome, the interpretation of secondary p-values, and the clinical relevance of the primary estimate.

The safety summary provides counts and selected event terms but not detailed event timing, attribution, or participant-level context. It is descriptive and based on a small study record. The registry information therefore supports a bounded statistical reading of the posted outcomes, not a complete assessment of all protocol, analysis, or safety details.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Study of the Effect of Ivacaftor on Lung Clearance Index in Subjects With Cystic Fibrosis and the G551D Mutation — NCT01262352.
• Registry record last updated 2013-02-11; status last verified 2013-02.
• Results first posted 2013-01-30.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

The registry describes a completed Phase 2 randomized, quadruple-masked, placebo-controlled crossover study of ivacaftor in participants aged 6 years and older with cystic fibrosis and the G551D-CFTR mutation on at least 1 allele. The official title specifies FEV1 >90% predicted. The study enrolled 21 participants.

The primary outcome was absolute change from baseline in LCI through Day 29. The sponsor's mixed models analysis reported a mean difference of -2.069, with a 95% confidence interval from -2.98 to -1.15. The unadjusted re-calculation was similar. Three secondary outcomes were posted, with differing estimates and precision.

The registry does not report the original sample-size justification, detailed model specification, missing-data handling, or multiplicity strategy. Those omissions qualify interpretation of the posted results and the secondary comparisons.