Study of Ivacaftor in Cystic Fibrosis Subjects Aged 12 Years and Older With the G551D Mutation: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study of Ivacaftor in Cystic Fibrosis Subjects Aged 12 Years and Older With the G551D Mutation (NCT00909532), a randomized phase 3 study. The primary outcome is Absolute Mean 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 a population defined by both diagnosis and mutation. That population definition matters to interpretation: the findings concern the trial participants meeting those criteria, rather than all people with cystic fibrosis. The comparison was between assignment to ivacaftor and assignment to placebo under the study conditions; the registry record does not establish how results would differ in other populations or settings.

The primary endpoint focused on change in percent predicted FEV1 over the period through Week 24. The registry also lists later lung-function assessment and other secondary outcomes, including respiratory-domain questionnaire score, sweat chloride concentration, time to first pulmonary exacerbation, and weight. Results for most of those secondary outcomes are not reported in the registry record. The central statistical question, therefore, is the size and precision of the posted primary comparison, not whether every outcome important to patients or clinicians moved in the same way.

3. Trial Design

This was a Phase 3 randomized, double-blind, placebo-controlled, parallel-group study sponsored by Vertex Pharmaceuticals Incorporated. The registry record gives enrollment as 167 and status as completed. The study started in 2009-06, and primary completion was 2010-07. Participants were assigned to placebo or 150 mg ivacaftor every 12 hours, with treatment described as continuing for up to 48 weeks. The record specifies quadruple masking; it does not describe the identities of all masked parties in the information available for this analysis.

The primary outcome was change from baseline in percent predicted FEV1 through Week 24. Its analysis population included all randomized participants who received at least 1 dose and had available assessments during the time frame. The posted arm-level outcome counts are 78 for placebo and 83 for ivacaftor. These are the counts attached to the outcome estimates, and need not be treated as a description of every stage of participant flow. Further details about exclusions, missing assessments, and the handling of individual missing values are not reported in the registry record.

The trial was parallel group, so the posted comparison is between groups assigned to different treatments rather than a crossover comparison within the same participant. Randomization is intended to make treatment groups comparable on average at the point of assignment, though it cannot guarantee identical groups on every characteristic. The record does not report the randomization ratio, blocking or stratification factors, or the exact sequence-generation and concealment procedures.

The registry identifies the primary endpoint’s reported quantity as a least-squares mean and its dispersion as a standard error. It also reports the sponsor’s primary comparison as a mixed models analysis of mean difference in final values. The complete model specification, covariate adjustments, assumptions about repeated measurements, and original design calculations are not reported in the registry record. Consequently, the posted result can be interpreted as a randomized-group comparison, while details beyond those explicitly described should not be inferred.

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 167 subjects were randomized; 161 subjects received at least 1 dose of the study drug. A 2-week run-in period was included to establish the baseline assessments on Day 1 after ensuring that subjects were properly taking their cystic fibrosis (CF) medication regimens.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: All randomized subjects who received at least 1 dose of study drug (ivacaftor or placebo) 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 Mean Change From Baseline in Percent Predicted Forced Expiratory Volume in 1 Second (FEV1) Through Week 24, measured over baseline through 24 weeks.

The primary endpoint is the absolute mean change from baseline in percent predicted forced expiratory volume in 1 second (FEV1) through Week 24. FEV1 is the amount of air a person can forcefully exhale in the first second of a breathing test. The registry describes spirometry as a standardized assessment of lung function and notes that FEV1 is widely used as an endpoint in cystic fibrosis studies.

Expressing FEV1 as percent predicted relates a measurement to a predicted value, rather than presenting only an unscaled volume. Change from baseline focuses on how the measure shifted during the study relative to each participant’s baseline assessment. The reported group estimates are least-squares means, which are model-based means; the registry’s description does not provide enough detail to specify all adjustments used to obtain them.

The endpoint is continuous, so the main summary is a mean change rather than a count of participants meeting a responder threshold. The posted group estimates are -0.2 for placebo and 10.4 for ivacaftor, with a reported mean difference of 10.6. These values describe the measured change over the stated period and should be interpreted with the uncertainty interval and analysis method, not as a guarantee of an individual participant’s change. The registry record does not report a threshold defining a clinically important change in this measure.

7. Results Posted in the Registry

• 150 mg Ivacaftor q12h: mean 10.40 versus -0.20 on control; difference 10.60 (95% CI 8.66 to 12.54), standardized effect d = 1.69; 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 Mean Change From Baseline in Percent Predicted FEV1 Through Week 48

• 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:
  • 150 mg Ivacaftor q12h: mean 10.10 versus -0.40 on control; difference 10.50 (95% CI 8.56 to 12.44), standardized effect d = 1.67; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for 150 mg Ivacaftor q12h than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry lists secondary measures covering lung function through Week 48, respiratory-domain questionnaire score, sweat chloride concentration, time to first pulmonary exacerbation, and weight. The posted Week 48 FEV1 result has the same broad direction as the primary Week 24 comparison: the mean change estimate favors the ivacaftor group. This provides a later assessment of the same lung-function measure, but it remains secondary to the designated primary endpoint.

Results for the other listed secondary outcomes are not reported in the registry record. As a result, the available results cannot establish a consistent pattern across respiratory symptoms, sweat chloride, exacerbations, and weight. The absence of a posted result should not be interpreted as evidence that there was no difference, nor as evidence of a difference. It means that the registry record does not provide the estimates needed to assess those outcomes.

Secondary results generally carry less evidential weight than a prespecified primary result because trials may examine multiple outcomes and time points. When many comparisons are considered, the chance of obtaining at least one apparently notable result by chance can increase. Adjustments or a prespecified hierarchy can address aspects of this issue, but the registry record does not report a multiplicity strategy. Consequently, any unadjusted secondary p-values, if available elsewhere, would need cautious interpretation and should not be treated as equivalent to the primary analysis.

The secondary outcomes also differ in what they measure and in their analysis structure. A continuous measure, a time-to-event outcome, and a questionnaire score do not answer identical questions. The posted Week 48 lung-function pattern can add context about the primary measure over a longer period, but it cannot substitute for results on other domains or establish the overall balance of benefit and harm. A complete account of the secondary outcome evidence is not reported in the registry record.

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

• Absolute Mean Change From Baseline in Percent Predicted FEV1 Through Week 48
• Absolute Change From Baseline in Cystic Fibrosis Questionnaire-Revised (CFQ-R) Score Through Week 24 and Week 48 (Respiratory Domain Score, Pooled)
• Absolute Change From Baseline in Sweat Chloride Concentration Through Week 24 and Week 48
• Time-to-first Pulmonary Exacerbation Through Week 24 and Week 48
• Absolute Change From Baseline in Weight at Week 24 and Week 48

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous, and the reported group summaries are least-squares means with standard errors. A mean summarizes the central value of a continuous measurement across participants; a standard error describes the uncertainty in estimating that mean, rather than the spread of individual participant measurements. The registry’s group estimates are therefore not measures of how variable participants’ FEV1 changes were. The posted analyses report 78 participants for placebo and 83 for ivacaftor.

What does the sponsor’s mixed models analysis represent?

The registry reports a mixed models analysis of the mean difference in final values. In general, mixed models can analyze outcome measurements while accounting for relationships among repeated measurements from the same participant and can represent variation at more than one level. The specific model structure, covariates, covariance assumptions, and missing-data assumptions for this trial are not reported in the registry record. It is therefore not possible to reconstruct the sponsor’s full analysis from the brief method label alone.

The sponsor’s reported comparison is 10.6, with a 95% confidence interval from 8.6 to 12.6 and p < 0.001. The posted group estimates describe change from baseline, while the sponsor’s parameter is labelled mean difference in final values. These summaries are close in their reported magnitude, but their labels and methods should not be conflated. The sponsor’s analysis is the trial’s reported inferential result; the registry record does not include enough model detail to independently reproduce it exactly.

What is the recalculated comparison?

The recalculated result is a simple, unadjusted comparison based on the posted summary statistics. It gives a mean difference of 10.6, with an interval from 8.66 to 12.54 and p < 0.001. This calculation is not a reconstruction of the mixed models analysis. It uses the available group summaries to give a transparent approximation of the difference and its uncertainty, without the full participant-level data or the sponsor’s model specification.

The recalculation uses standard errors to approximate the underlying group variability, as indicated in the analysis details. That approximation can support an illustrative comparison, but it is not equivalent to fitting the trial’s original model. It also does not incorporate any unreported adjustment or model feature. The registry record marks no discrepancy between the recalculated and reported results. The two estimates and intervals are similar, but that similarity does not make the methods identical.

How should the p-values be read?

A p-value is calculated under a statistical model that represents a null hypothesis, commonly no average difference between groups. A small p-value means that data at least as extreme as the observed data would be relatively unusual under that model, assuming its conditions are appropriate. It is not a measure of effect size, clinical importance, or the probability that a hypothesis is true. The sponsor’s and recalculated p-values have different reported thresholds; they should be read in the context of their respective analyses rather than treated as exact interchangeable quantities.

Confidence intervals give a range of values compatible with the data under a specified analysis and its assumptions. In repeated use of the same method under the same conditions, intervals at a stated confidence level would contain the target parameter at the stated rate. For this trial, the reported interval is centered around a positive mean difference and does not include zero. That supports a statistically discernible difference under the reported analysis, while uncertainty about the exact size remains.

Why do analysis populations and missing assessments matter?

The primary population is described as randomized participants who received at least 1 dose and had available assessments during the time frame. This is not simply everyone enrolled: the population definition conditions inclusion on receiving study drug and having an available assessment. Randomization supports a fair group comparison at assignment, but restricting analysis to participants with post-assignment observations can affect that balance if availability is related to treatment or outcome. The registry record does not report the number of participants excluded from the primary analysis, reasons for unavailable assessments, or sensitivity analyses addressing missing data.

In general, missing-data methods matter because analyses may rely on assumptions about the outcomes that were not observed. A model may use available repeated measurements under stated assumptions, but those assumptions cannot be evaluated without the model description and missingness information. Neither the exact missing-data strategy nor the extent of missingness is reported in the registry record. The primary results should therefore be read as estimates for the stated analysis population, rather than assumed to be a complete outcome for every randomized participant.

Finally, the study’s sample-size planning assumptions, interim analyses, and complete prespecified statistical plan are not reported in the registry record. The sample-size illustrations associated with the observed result are not a substitute for the original design rationale. Without the original plan, it is not possible to assess from this record whether every analytic decision, endpoint, or time point followed a prespecified procedure.

11. Confidence Intervals and Precision

The sponsor reports a 95% confidence interval for the primary mean difference from 8.6 to 12.6. The unadjusted recalculation gives an interval from 8.66 to 12.54. These intervals are close, and both exclude zero. Their narrow span relative to the point estimate indicates that, under the respective analysis assumptions, the estimated average difference is more precisely located than it would be with a much wider interval. The interval still does not identify the exact effect for the population or for any individual participant.

In general, a confidence interval represents uncertainty in an estimate. It is not a range containing a stated proportion of individual participant responses, and it is not a probability statement about the fixed treatment effect after the data have been observed. A 95% interval is generated by a method that, under its assumptions, would cover the target parameter in 95% of repeated applications. Interpretation depends on the model and data conditions used to construct it.

The small difference between the sponsor’s interval and the recalculated interval reflects the fact that the reported sponsor analysis and the simple unadjusted calculation are not identical procedures, as well as differences in rounding. The recalculated endpoints are printed to two decimal places, while the sponsor’s are printed to one decimal place. Neither presentation removes uncertainty related to unreported model specifications, missing assessments, or the trial’s selected population.

The point estimate and interval address statistical precision, not clinical importance. The registry record does not report a minimal important difference or a responder threshold for this endpoint. It also does not provide enough detail to evaluate whether uncertainty from multiple outcome testing or all potential model choices is represented in the interval. The confidence interval is thus useful for understanding the primary estimate’s statistical uncertainty, but it should not be read as a complete account of every source of uncertainty.

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 display gives planning illustrations in participants per arm, not total events. The illustrations assume a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. They use the observed effect as a reference and show planning for 100%, 75%, and 50% of that observed effect. The trial’s own original design assumptions are not reported in the registry record; these displayed assumptions belong to the planning illustration, not necessarily to the trial design.

The column for 80% power gives the illustrative number of participants per arm for a design with an 80% chance of detecting the specified effect under the stated assumptions, if that effect and the model assumptions hold. The 90% power column uses a higher target probability of detecting that same specified effect and generally requires more participants per arm. These are design-planning quantities, not observed characteristics of the enrolled trial groups.

Rows based on a smaller fraction of the observed effect require more participants per arm than rows based on the full observed effect. In general, smaller effects are harder to distinguish from random variation, so a larger study is needed to achieve the same target power under otherwise similar assumptions. The display illustrates this relationship using the stated fractions; it does not establish what effect would be expected in a future study or what sample size would be appropriate under a different design.

This is not observed power. Observed power is not a measure of how convincing the result is after the data are known; the uncertainty interval and estimated effect are more informative for that purpose. The illustrations are best read as conditional planning examples based on the observed result, not as evidence that the original trial was designed using these assumptions or that it had a particular probability of success.

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 = 10.600; pooled standard deviation σ = 6.284.
2. n = 2 × (1.96 + 0.842)² × 6.284² / 10.600² = 5.5, 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 <- 10.6                      # observed difference in means
sigma <- 6.28359148995052                     # 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(909532)
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 = 10 (80% power), 14 (90% power)
 50% of observed effect: n per arm = 23 (80% power), 30 (90% power)
power.t.test: 6.6 
Simulated power at n = 6 per arm: 0.755 (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 primary analysis is reported as a mixed models analysis of mean difference in final values. It estimates a difference of 10.6, with a 95% confidence interval from 8.6 to 12.6 and p < 0.001. The simple unadjusted recalculation from the posted summary statistics also gives a difference of 10.6, with an interval from 8.66 to 12.54 and p < 0.001. The estimates are closely aligned, although the analyses are not interchangeable and the interval endpoints and p-value thresholds differ.

The sponsor’s result should be understood as the trial’s reported inferential analysis. The recalculation is an approximation from group summaries, not a re-creation of the mixed models analysis. The registry record does not include the full model specification or participant-level data needed to reproduce the sponsor’s calculation. There is no reported discrepancy between the two results, and the recalculation is useful as a transparent check on the posted summary rather than a replacement for the sponsor’s analysis.

Both reported intervals lie above zero, and both analyses indicate a positive average difference between groups under their respective methods. That agreement supports the conclusion that the broad statistical reading is not sensitive to the distinction between these two presentations. It does not resolve questions about missing data, model assumptions, multiplicity, or clinical importance, for which additional information is not reported in the registry record.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study evaluates multiple outcomes, time points, groups, or statistical comparisons. If each is tested separately without an appropriate plan, the chance of at least one result appearing statistically notable by chance can be greater than for a single prespecified test. The registry lists several secondary outcomes and reports a primary endpoint, but the multiplicity plan, any testing hierarchy, and any adjustment to the reported significance levels are not reported in the registry record. The primary p-value should therefore be interpreted as the result of its stated analysis, without assuming that it was or was not adjusted for other testing.

Missing outcome data can also affect interpretation. The primary analysis population is defined as randomized participants who received at least 1 dose and had available assessments during the time frame. The registry record does not state how many randomized participants lacked assessments, why assessments were unavailable, or how missing values were handled in the sponsor’s model. It also does not report sensitivity analyses under alternative assumptions about missing outcomes. These details matter because a comparison among participants with observed assessments may differ from the comparison that would have been obtained had all randomized participants contributed complete data.

The analysis population is not described as every enrolled participant regardless of treatment receipt or assessment availability. That distinction should be kept in view when interpreting the randomized comparison. The exact numbers screened, assigned, treated, and included at each analysis stage, along with a full participant-flow account, are not reported in the registry record. The posted outcome counts indicate the analyzed group sizes for this endpoint, but do not explain the participant-level flow that led to them.

The registry record also does not report interim analyses, a complete statistical analysis plan, or the original sample-size justification. These omissions prevent an assessment of whether the outcome hierarchy, stopping considerations, missing-data choices, and model details were fully prespecified. They do not invalidate the reported result, but they limit independent evaluation of how the inferential procedures were selected and whether all planned analyses are represented.

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 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: cystic fibrosis lung (33.3%), hemoptysis (5.1%), hypoglycaemia (2.4%), atrioventricular block complete (1.3%), gastrooesophageal reflux disease (1.3%).

The registry reports participants with serious adverse events as 33 of 78 in the placebo group and 20 of 83 in the 150 mg ivacaftor group. These are counts of participants affected, not counts of all individual events; one participant may experience more than one event. The registry also reports other adverse events affecting 78 of 78 placebo participants and 82 of 83 ivacaftor participants. The deaths field has no reported count, so deaths are not reported in the registry record.

The listed serious-event terms include cystic fibrosis lung, hemoptysis, hypoglycaemia, atrioventricular block complete, gastrooesophageal reflux disease, and vomiting, with the displayed percentages attached to those terms in the registry record. The list should not be interpreted as a complete account of every event or as proof that an event was caused by study treatment. The record does not provide event-level narratives or enough comparative detail to establish causality.

These figures are descriptive safety summaries. They do not provide a formal estimate of risk adjusted for follow-up or other factors, and the registry record does not report a comparative statistical analysis for serious adverse events. The counts should therefore be read alongside the study duration and population, without treating them as a complete assessment of safety.

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

The primary result describes a difference in average change in percent predicted FEV1 between the randomized groups through Week 24. Under the posted analyses, the mean difference is positive, its confidence interval lies above zero, and the sponsor reports p < 0.001. The result is statistically distinguishable from zero under the reported model, while still carrying uncertainty about the exact size of the average difference.

It does not mean that every participant experienced a change equal to the group average. Group means conceal individual variation, and the registry does not report the proportion of participants who reached a particular level of change. The record also gives no threshold for a clinically important difference. Statistical precision cannot, on its own, determine whether a measured difference is important to participants or how it relates to their day-to-day experience.

The result applies directly to the study population and conditions described: people aged 12 years and older with cystic fibrosis and the G551D mutation, assigned to ivacaftor or placebo under the trial design. The registry record does not establish that the same estimate applies to people with other mutations, people outside the studied age group, or different treatment regimens and follow-up periods. Generalizing beyond the participants and study conditions requires evidence not contained in this result alone.

Nor does the primary lung-function outcome answer every question about treatment. The registry lists other outcomes, but results for most of them are not reported in the registry record. The posted data therefore do not establish a complete pattern across symptoms, exacerbations, sweat chloride, weight, and safety. The serious adverse event counts are descriptive and do not provide a full causal or comparative safety assessment.

In short, the posted statistics support a positive average between-group difference in the primary FEV1 outcome, with an interval that indicates relatively good statistical precision under the stated analyses. They do not by themselves establish individual response, clinical importance, effects in unstudied groups, or the overall balance of all outcomes. Those questions require context and information beyond the primary estimate.

18. Why This Trial Matters Statistically

This trial illustrates how a randomized comparison can connect a clinically familiar measurement to a clearly defined statistical estimand. The primary endpoint is a continuous lung-function measure, and the registry reports group changes, a between-group difference, uncertainty intervals, and a sponsor analysis. Reading these quantities together is more informative than focusing only on whether a p-value crosses a conventional threshold: the difference describes magnitude, while the interval describes statistical uncertainty under the analysis assumptions.

It also demonstrates why the method label matters. The registry reports a mixed models analysis, while the accompanying recalculation is an unadjusted approximation from summary statistics. Similar estimates can provide a useful check, but the approximation does not reproduce the sponsor’s full procedure. Without participant-level data and model details, the reported analysis cannot be reconstructed exactly. Clear distinctions between a trial’s reported result and a summary-statistic calculation help prevent an illustrative check from being mistaken for the original analysis.

The record also shows the limits of a statistically precise primary result. A confidence interval can narrow uncertainty about an average while leaving important questions unanswered about clinical importance, individual variation, missing data, multiplicity, and outcomes not reported in the registry record. The Week 48 lung-function result adds a later observation on the same measure, but does not fill gaps in other secondary outcomes.

Finally, sample-size illustrations based on the observed effect are not evidence about the original design or the probability that this trial succeeded. Distinguishing planning calculations from trial results, and separating reported analyses from approximate recalculations, are core statistical reading skills. This record offers a concrete example of both the value and the limits of the information contained in a registry result.

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 trial population was defined by cystic fibrosis, age 12 years and older, and the G551D mutation. The results should not automatically be extended to other mutation groups or populations. The registry record does not provide enough information to evaluate how representative the participants were of the broader population meeting those criteria, or how the study’s eligibility requirements affected generalizability.

The primary outcome is a spirometry measure, and the registry describes it as widely used in cystic fibrosis studies. However, no threshold for a clinically important change is reported. The registry also does not provide the distribution of participant-level changes or the proportion meeting a response criterion. Consequently, the group mean cannot show how consistently participants’ outcomes varied around that average or how the difference maps to a meaningful change for an individual.

Although treatment was described for up to 48 weeks, the primary comparison concerns the period through Week 24. The record includes a Week 48 FEV1 result, but results for most other listed secondary outcomes are not reported. The available information therefore does not establish a complete longer-term account across lung function, respiratory symptoms, sweat chloride, exacerbations, weight, and safety.

Important analytic details are also absent. The complete mixed-model specification, the extent and reasons for missing assessments, the missing-data strategy, sensitivity analyses, multiplicity plan, interim analyses, and original sample-size justification are not reported in the registry record. The primary analysis population required treatment receipt and available assessments, so the interpretation pertains to that defined group; the record does not provide a full participant-flow account to assess how it differs from all randomized participants.

Safety reporting is limited to posted participant counts and listed serious-event terms. The registry does not report deaths, event-level detail, or a formal comparative safety analysis. These limitations do not negate the primary estimate, but they restrict what can be concluded about its clinical meaning, broader applicability, and the trial’s full outcome profile.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Study of Ivacaftor in Cystic Fibrosis Subjects Aged 12 Years and Older With the G551D Mutation — NCT00909532.
• Registry record last updated 2013-01-18; status last verified 2013-01.
• Results first posted 2012-08-21.
• 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

NCT00909532 is a completed Phase 3 randomized, double-blind, placebo-controlled, parallel-group study sponsored by Vertex Pharmaceuticals Incorporated. It enrolled 167 people with cystic fibrosis aged 12 years and older who had the G551D mutation. Participants received placebo or 150 mg ivacaftor every 12 hours, for up to 48 weeks.

The primary endpoint was change from baseline in percent predicted FEV1 through Week 24. The posted mean difference was 10.6. The sponsor’s mixed models analysis reported a 95% confidence interval from 8.6 to 12.6 and p < 0.001; the unadjusted recalculation was similar. The Week 48 FEV1 result had a consistent direction, while results for most other listed secondary outcomes are not reported in the registry record.

The primary finding is a positive average difference under the reported analyses. The record does not report a clinically important threshold, full model and missing-data details, a multiplicity plan, or a complete comparative safety analysis. Interpretation is therefore strongest for the stated primary outcome and trial population, with broader conclusions limited by what is not reported.