Ciprofloxacin Dry Powder for Inhalation in Non-cystic Fibrosis Bronchiectasis (Non-CF BE): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Ciprofloxacin Dry Powder for Inhalation in Non-cystic Fibrosis Bronchiectasis (Non-CF BE) (NCT01764841), a randomized phase 3 study. The primary outcome is Time to First Exacerbation Event Within 48 Weeks.

2. Clinical Question

The statistical question is about the timing of a first qualifying event, not simply whether a participant experienced any respiratory symptom. The trial’s event definition combines treatment for an exacerbation with clinical features, and the endpoint follows participants from randomization until the first recorded qualifying event. This makes the comparison one of event timing over follow-up. It does not, by itself, describe the total number of events per participant, the severity of every event, or how participants felt across the entire follow-up period. Those topics appear among the listed secondary outcomes, but their results are not all posted in the registry record.

3. Trial Design

The registry record describes a completed phase 3, randomized, double-blind, placebo-controlled, multicenter, parallel-group study. Masking is recorded as quadruple. Enrollment was 416 participants, and the primary analysis population was the full analysis set, which included randomized participants. The study began on 2013-05-02, and primary completion was recorded as 2016-03-09.

Participants were assigned to intermittent ciprofloxacin dry powder for inhalation or matched placebo. Ciprofloxacin was administered twice daily. The 28-day schedule used 28 days of treatment followed by 28 days off treatment, while the 14-day schedule used 14 days on followed by 14 days off. Both schedules were planned for a 48-week treatment phase. The record describes six cycles for the 28-day schedule and twelve active cycles for the 14-day schedule. The placebo preparations followed the corresponding schedules.

The primary result compares each active schedule with pooled placebo. The posted analysis includes 141 participants in the 28-day ciprofloxacin group, 137 in the 14-day ciprofloxacin group, and 138 in pooled placebo for the time-to-event outcome. The registry’s safety population counts differ slightly from these primary analysis counts, so those denominators should be read separately rather than treated as interchangeable.

The registry record does not report details of the randomization procedure, allocation concealment, study locations, eligibility criteria beyond the condition description, or how participants were assigned among the two active schedules and placebo schedules. The original sample-size justification and trial-specific statistical analysis plan are not reported in the registry record. The posted information therefore establishes the broad randomized design and schedules, but it does not fully document how design choices were implemented or planned statistically.

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: Overall 902 participants were screened, of them 486 were screen failures, and 416 were randomized, out of which 414 participants were assigned to the treatment. One participant from Ciprofloxacin 14 Days on/off group and one participant from Placebo 28 Days on/off group did not receive the study treatment after initial screening.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full analysis set (FAS) included participants who were randomized.

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 Time to First Exacerbation Event Within 48 Weeks, measured over Up to Week 48.

The primary endpoint was time to first exacerbation event within 48 weeks, reported in days. It measured the interval from randomization until the visit at which the investigator recorded the first qualifying exacerbation. The event definition required systemic antibiotic use, fever or malaise or fatigue, and worsening of at least three signs or symptoms. The registry reports a median time for groups where the value was posted, alongside confidence limits where available, and reports hazard ratios for the comparisons with pooled placebo.

A time-to-event endpoint is useful when the timing of an event matters and when participants may have different follow-up experiences. It can use information about when a first event occurs, rather than reducing all follow-up to a yes-or-no event count. The hazard ratio summarizes the relative event rate over follow-up under the assumptions of the analysis; it is not the ratio of the group medians, nor does it directly state how many days an individual participant might gain or lose.

The endpoint is also narrower than the broader study aim of evaluating exacerbation frequency. Once a participant has a first event, later exacerbations do not change the time-to-first-event endpoint. The registry lists other exacerbation outcomes separately, including counts of participants with worsening of specified numbers of signs or symptoms. The time-to-first-event result should therefore be interpreted as evidence about the first qualifying event during the follow-up period, not as a complete account of recurrent exacerbations, symptoms, or quality of life.

7. Results Posted in the Registry

• Ciprofloxacin DPI 28 Days on/Off (Cipro 28) vs Pooled Placebo: hazard ratio 0.73 (95% CI 0.50–1.07), reported p = 0.065 (as reported in the registry).
• Ciprofloxacin DPI 14 Days on/Off (Cipro 14) vs Pooled Placebo: hazard ratio 0.53 (95% CI 0.36–0.80), reported p < 0.001 (as reported in the registry).

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.

Mean Change From Baseline in Patient Reported Outcome Saint George's Respiratory Questionnaire (SGRQ) Symptoms Component Score at End of Treatment (Week 44/46)

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Ciprofloxacin DPI 28 Days on/Off (Cipro 28): mean -8.17 versus -4.23 on control; difference -3.94 (95% CI -10.97 to 3.09), standardized effect d = -0.18; z-test p = 0.272.
  • Ciprofloxacin DPI 14 Days on/Off (Cipro 14): mean -7.20 versus -4.23 on control; difference -2.97 (95% CI -9.88 to 3.94), standardized effect d = -0.15; z-test p = 0.400.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Ciprofloxacin DPI 28 Days on/Off (Cipro 28) and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Ciprofloxacin DPI 14 Days on/Off (Cipro 14) and the control. The interval gives the range of effects that remain compatible with the data.

Mean Change From Baseline in Patient Reported Outcome Quality of Life Questionnaire for Bronchiectasis (QoL-B) Respiratory Symptoms Domain Score at End of Treatment (Week 44/46)

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Ciprofloxacin DPI 28 Days on/Off (Cipro 28): mean 7.70 versus 8.22 on control; difference -0.52 (95% CI -6.47 to 5.43), standardized effect d = -0.03; z-test p = 0.864.
  • Ciprofloxacin DPI 14 Days on/Off (Cipro 14): mean 6.72 versus 8.22 on control; difference -1.50 (95% CI -7.53 to 4.53), standardized effect d = -0.09; z-test p = 0.626.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Ciprofloxacin DPI 28 Days on/Off (Cipro 28) and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Ciprofloxacin DPI 14 Days on/Off (Cipro 14) and the control. The interval gives the range of effects that remain compatible with the data.

Mean Change From Baseline in Forced Expiratory Volume in One Second (FEV1) at End of Treatment (Week 44/46)

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Ciprofloxacin DPI 28 Days on/Off (Cipro 28): mean -0.01 versus 0.02 on control; difference -0.04 (95% CI -0.14 to 0.07), standardized effect d = -0.16; z-test p = 0.498.
  • Ciprofloxacin DPI 14 Days on/Off (Cipro 14): mean -0.03 versus 0.02 on control; difference -0.05 (95% CI -0.16 to 0.06), standardized effect d = -0.19; z-test p = 0.373.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Ciprofloxacin DPI 28 Days on/Off (Cipro 28) and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Ciprofloxacin DPI 14 Days on/Off (Cipro 14) and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover several different dimensions: whether exacerbation events involved worsening of specified numbers of signs or symptoms, pathogen findings, respiratory symptoms and quality of life, and lung function. The posted continuous outcomes include changes in SGRQ symptoms, QoL-B respiratory symptoms, and FEV1. The pattern across the recalculated comparisons is not a uniform separation between active treatment and placebo: the estimated mean differences are close to zero relative to the uncertainty intervals, and the intervals include zero. These comparisons are unadjusted recalculations rather than sponsor-reported analyses.

That overall pattern does not directly confirm or contradict the primary time-to-first-event result. The endpoints measure different things: delaying a first qualifying exacerbation is not the same as changing a symptom score, respiratory quality-of-life domain, or FEV1 by the end of treatment. Nor are mean changes in these outcomes a substitute for recurrent-event outcomes. The secondary findings therefore add context, but they should not be collapsed into one overall claim about treatment effects.

The registry lists seven secondary outcomes, while not all have results represented in the posted result summaries used for this analysis. For secondary outcomes without posted results, findings are not reported in the registry record. The absence of a posted estimate should not be interpreted as evidence of no difference.

Unadjusted secondary analyses carry less weight than a prespecified primary analysis because many outcomes and comparisons can create opportunities for chance findings. The registry record does not report whether multiplicity was controlled, how secondary endpoints were prioritized, or which analyses were prespecified. The lack of that information makes it difficult to assess how much confirmatory status any secondary result should receive. The most cautious reading is to regard these outcomes as supportive or exploratory context unless the registry record documents a planned analysis and a multiplicity strategy.

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

• Number of Participants With Exacerbation Events With Worsening of at Least Three Signs/Symptoms Over 48 Weeks
• Number of Participants With Exacerbation Events With Worsening of at Least One Sign/Symptom Over 48 Weeks
• Percentage of Participants With Pathogen Eradication at End of Treatment (Week 44/46)
• Mean Change From Baseline in Patient Reported Outcome Saint George's Respiratory Questionnaire (SGRQ) Symptoms Component Score at End of Treatment (Week 44/46)
• Percentage of Participants With Occurrence of New Pathogens Present at End of Treatment (Week 44/46)
• Mean Change From Baseline in Patient Reported Outcome Quality of Life Questionnaire for Bronchiectasis (QoL-B) Respiratory Symptoms Domain Score at End of Treatment (Week 44/46)
• Mean Change From Baseline in Forced Expiratory Volume in One Second (FEV1) at End of Treatment (Week 44/46)

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is a time-to-event outcome: each participant’s relevant observation is the time from randomization until a first qualifying exacerbation, or the end of observed follow-up without such an event. A participant without a recorded event by the end of observation is typically treated as censored in a time-to-event analysis. Censoring means that the event time is not known beyond the last point of follow-up; it does not mean that an event occurred at that time. The registry record does not give detailed information about censoring rules or handling of missing follow-up.

What the hazard ratio describes

A hazard is the instantaneous event rate among participants who have not yet experienced the event, considered over follow-up. A hazard ratio compares that rate between groups. A value below 1 indicates a lower estimated hazard in the first named group relative to its comparator, while a value above 1 indicates a higher estimated hazard. This is a relative, time-to-event summary; it is not a direct difference in median days, a risk ratio at a fixed time, or an estimate of the number of events prevented.

For this study, the registry reports hazard ratios for each ciprofloxacin schedule against pooled placebo. It identifies the method as a Wald-type test. In general, a Wald-type test compares an estimated effect with its uncertainty using an approximation to the sampling distribution of that estimate. The registry record does not report further detail about the exact model, covariate adjustment, proportional-hazards assessment, stratification, or any sensitivity analyses. Those features should not be inferred from the label of the test alone.

Why medians and hazard ratios differ

The median time to event is the time by which half of the relevant event-time distribution has experienced the event, under the survival-analysis estimation approach. It gives an interpretable point on the time scale. A hazard ratio instead summarizes relative event rates across follow-up. A median can be unavailable or imprecise when event-time information is limited, and a single median cannot describe the shape of the full event-time distribution. In this record, some median values or confidence limits are missing, so the reported hazard ratios are the more complete sponsor-reported comparative summaries.

A confidence interval expresses statistical uncertainty around an estimate under the assumptions of the analysis. A 97.5% interval describes a range of values compatible with the data and method at that confidence level; it is not a probability statement that the true value lies within the particular calculated interval. An interval crossing 1 for a hazard ratio includes the null value of no relative difference. An interval entirely below 1 does not, though interpretation still depends on the analysis plan and how multiple comparisons were addressed.

Unadjusted recalculations for continuous outcomes

The posted secondary results include mean changes in the SGRQ symptoms component, QoL-B respiratory symptoms domain, and FEV1. Recalculated comparisons for these outcomes are simple, unadjusted comparisons from the posted summary statistics, not the sponsor’s reported analyses. They compare the active-group mean with the corresponding placebo mean and use an estimated mean difference and confidence interval. Such calculations do not account for participant-level data, baseline covariates, repeated measurements, missing-data procedures, or any adjustment that may have been used in the trial analysis. The registry record lists no reported sponsor analyses for these continuous comparisons, so these re-calculations should be treated as descriptive statistical aids rather than replacements for a prespecified analysis.

The standard deviation describes variation among participant-level measurements around the group mean. A confidence interval for a mean difference reflects uncertainty in the difference estimate, which depends on group sizes and variability. When the interval is wide, it allows a broad range of effects. When it includes zero for a mean difference, the data are compatible with no average difference as well as with effects in either direction. These principles are general; clinical importance also depends on the outcome scale and what differences matter to participants, information not established by statistical significance alone.

Planning illustrations and dispersion

Sample-size illustrations use the observed effect as a planning reference and consider smaller fractions of that effect. In general, smaller effects are harder to distinguish from random variation and require more information, often through more participants or events. For time-to-event outcomes, the displayed planning quantities are total events, not participants per arm. For the continuous outcomes, they are participants per arm. These are planning illustrations based on the stated assumptions, not the trial’s original sample-size calculation.

Over-dispersion is a general concern when variability exceeds what a simple statistical model expects. In recurrent-event data, for example, participants can differ in their tendency to have repeated events, so the spread of counts may exceed a basic model’s assumptions. Methods that account for such variation can produce more appropriate uncertainty estimates. The primary endpoint is time to first exacerbation rather than a recurrent event count, and the registry record does not report a particular over-dispersion method. The concept is relevant to interpreting exacerbation-frequency analyses generally, but no such method should be attributed to this trial without documentation.

11. Confidence Intervals and Precision

The 28-day comparison’s hazard-ratio estimate was 0.733, with a 97.5% confidence interval from 0.503 to 1.069. The interval extends across 1, indicating that the data and analysis are compatible with both a lower hazard and a value slightly above the null. The reported p-value was 0.065. The estimate therefore has meaningful uncertainty, and the point estimate alone should not be read as a definitive measure of the treatment contrast.

The 14-day comparison’s hazard ratio was 0.533, with a 97.5% confidence interval from 0.357 to 0.797. This interval is narrower relative to its distance from 1 and remains below the null value. Its reported p-value was 0.001. The interval still allows a range of possible relative effects; it does not identify one exact effect that applies to every participant or at every time point.

For the median event times, the 28-day ciprofloxacin estimate was 336 days, with a lower confidence limit of 206 days; the upper confidence limit is not reported in the registry record. For the 14-day ciprofloxacin median, the estimate and upper confidence limit are not reported in the registry record, while the lower confidence limit is 290 days. Pooled placebo had a median of 186 days, with a confidence interval from 136 to 282 days. These incomplete intervals restrict direct assessment of precision for the median estimates.

Confidence intervals express uncertainty under the specified statistical method and its assumptions. They do not capture every source of uncertainty, such as limitations in outcome ascertainment, missing information, or choices in analysis. The registry record reports the primary comparison intervals but does not provide enough detail to assess all such sources. The contrast between the two confidence intervals is a description of the posted estimates, not a formal test that the two ciprofloxacin schedules differ from each other.

12. Planning a Similar Trial: Sample Size

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

The sample-size illustrations are planning calculations based on effects observed in this trial, not the trial’s original design calculation. The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two groups in a comparison, a normal approximation, and an effect to detect set to the stated fraction of the observed effect. For time-to-event comparisons, the quantities are total events required across the comparison. For the continuous outcomes, the quantities are participants per arm.

The 80% power column describes the number of events or participants that a hypothetical study would need, under those assumptions, to have an 80% chance of detecting the specified effect using the assumed test criterion. The 90% power column represents a higher chance of detection under the same planning framework, and therefore generally requires more information. These descriptions concern prospective design performance under assumptions; they are not probabilities that the observed trial result is correct.

The rows considering 100%, 75%, and 50% of the observed effect illustrate how required information changes when the target effect becomes smaller. A smaller effect is harder to distinguish from random variation, so the planning calculation calls for more events or participants. For example, the time-to-event illustration for the 14-day comparison gives 80 events for 80% power when targeting 100% of the observed effect, compared with 318 events when targeting 50%. For the SGRQ comparison of the 28-day schedule, the corresponding participant-per-arm figures are 491 and 1,962. These examples illustrate the planning pattern; they are not evidence about what the trial was powered to detect.

For continuous outcomes, the displayed requirements are per arm, not totals across both groups. The registry record does not report the assumptions used in the trial’s own original sample-size justification. The planning figures are not observed power: they are hypothetical sample-size requirements under stated assumptions, and they should not be used to reinterpret the observed result as a 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

d is the total number of events needed (Schoenfeld's formula) with 1:1 allocation and proportional hazards.

Worked calculation for this trial

1. Hazard ratio HR = 0.733, so ln(HR) = -0.3105.
2. d = 4 × (1.96 + 0.842)² / [ln(0.733)]² = 325.7, rounded up to 326 events in total 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
hr <- 0.7331                              # observed hazard ratio
events_needed <- function(power, frac = 1) ceiling(round(4 * (z_a + qnorm(power))^2 / log(hr^frac)^2, 6))   # Schoenfeld, 1:1 allocation
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: events = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(events_needed(0.80, f), big.mark = ","), format(events_needed(0.90, f), big.mark = ",")))

# Simulation: given d total events under proportional hazards, events in the treatment arm are Binomial(d, hr / (1 + hr)).
# The score (log-rank type) statistic is (D1 - d / 2) / sqrt(d / 4).
set.seed(1764841)
d    <- events_needed(0.80)
reps <- 20000
D1 <- rbinom(reps, d, hr / (1 + hr))
z  <- (D1 - d / 2) / sqrt(d / 4)
cat(sprintf("Simulated power with %s events: %.3f (%d replicates)\n", format(d, big.mark = ","), mean(abs(z) > z_a), reps))

Output from running the code

100% of observed effect: events = 326 (80% power), 437 (90% power)
 75% of observed effect: events = 580 (80% power), 776 (90% power)
 50% of observed effect: events = 1,303 (80% power), 1,745 (90% power)
Simulated power with 326 events: 0.800 (20000 replicates)

The simulation uses the fact that, with d events in total and proportional hazards, the number of events in the treatment arm is binomial. It is an approximation that conditions on the total number of events, and it should land close to the target power.

14. Group-Sequential Design Analysis

Many time-to-event trials, especially in oncology, stop or report early when interim data are overwhelming, so a single fixed-sample number understates the real design problem. The calculation below is an illustrative group-sequential design built from this trial's posted control median and hazard ratio. The registry record does not state the planned number of looks or the spending function, so the design is a planning illustration, not a reconstruction of the protocol. Assumed: one-sided α = 0.025, 90% power, three equally spaced looks on information, Lan-DeMets O'Brien-Fleming spending, 24 months of accrual, 60 months in total and a 1% monthly dropout hazard.

Under these assumptions the design needs about 491 participants in total, with the boundaries below.

Fixed design versus group-sequential alternatives

Group-sequential designs cost a small increase in maximum sample size and events compared with the fixed design, in exchange for the chance to stop early for overwhelming efficacy. O'Brien-Fleming spending keeps early boundaries very conservative and the final boundary close to the fixed-design value, whereas Pocock spending spends more alpha early.

Sensitivity to a smaller true effect

Planning for exactly the observed effect is optimistic, because observed effects in published trials tend to be somewhat larger than the true effect. The table repeats the main design (three looks, O'Brien-Fleming spending, 90% power) for smaller true hazard ratios.

For context, this trial enrolled 416 participants.

Cross-check, upper boundaries: gsDesign 3.71, 2.511, 1.993 | rpact 3.71, 2.511, 1.993. Agreement between the two packages confirms the boundary calculation.

R code and output

suppressWarnings(suppressMessages({ library(gsDesign); library(rpact) }))
med_control <- 6.11506849315068          # control-arm median, months (converted from the posted unit)
hr          <- 0.7331          # hazard ratio used for planning
lambdaC     <- log(2) / med_control
eta         <- 0.01               # dropout hazard per month (assumption)
acc_months  <- 24                 # accrual duration (assumption)
study_months<- 60                 # total study duration (assumption)

design <- function(k, sfu, beta, h = hr) gsSurv(k = k, test.type = 1, alpha = 0.025, beta = beta, sfu = sfu,
  lambdaC = lambdaC, hr = h, hr0 = 1, eta = eta, gamma = 1, R = acc_months, T = study_months, minfup = study_months - acc_months)

# Main design: 3 looks, Lan-DeMets O'Brien-Fleming spending, one-sided alpha 0.025, 90% power
x <- design(3, sfLDOF, 0.10)
cat(sprintf("N_TOTAL|%s\n", format(ceiling(sum(x$gamma * x$R)), big.mark = ",")))
for (i in 1:3) cat(sprintf("GS|%d|%.1f|%.0f|%.3f|%.5f|%.5f\n", i, x$T[i], x$n.I[i], x$upper$bound[i], pnorm(-x$upper$bound[i]), cumsum(x$upper$spend)[i]))
cat("\n"); print(gsBoundSummary(x))

# Comparison of designs
cmp <- list(list("Fixed design, one analysis", 1, sfLDOF), list("Two looks, O'Brien-Fleming", 2, sfLDOF),
            list("Three looks, O'Brien-Fleming", 3, sfLDOF), list("Three looks, Pocock", 3, sfLDPocock))
cat("\n")
for (b in c(0.20, 0.10)) for (d in cmp) {
  y <- design(d[[2]], d[[3]], b)
  cat(sprintf("DES|%s|%d|%.0f|%s|%.1f\n", d[[1]], round(100 * (1 - b)), tail(y$n.I, 1), format(ceiling(sum(y$gamma * y$R)), big.mark = ","), tail(y$T, 1)))
}

# Sensitivity: what if the true effect is smaller than the observed one? (3 looks, O'Brien-Fleming, 90% power)
cat("\n")
for (fr in c(1, 0.75, 0.5)) {
  y <- design(3, sfLDOF, 0.10, exp(log(hr) * fr))
  cat(sprintf("SENS|%.2f|%.3f|%.0f|%s\n", fr, exp(log(hr) * fr), tail(y$n.I, 1), format(ceiling(sum(y$gamma * y$R)), big.mark = ",")))
}

# Independent cross-check of the boundaries with rpact
r <- getDesignGroupSequential(kMax = 3, alpha = 0.025, beta = 0.10, sided = 1, typeOfDesign = "asOF", informationRates = x$timing)
cat(sprintf("\nCross-check, upper boundaries: gsDesign %s | rpact %s\n", paste(round(x$upper$bound, 3), collapse = ", "), paste(round(r$criticalValues, 3), collapse = ", ")))

Method: LachinFoulkes 
    Analysis               Value Efficacy
   IA 1: 33%                   Z   3.7103
      N: 318         p (1-sided)   0.0001
 Events: 147        ~HR at bound   0.5420
   Month: 15    P(Cross) if HR=1   0.0001
             P(Cross) if HR=0.73   0.0338
   IA 2: 67%                   Z   2.5114
      N: 492         p (1-sided)   0.0060
 Events: 294        ~HR at bound   0.7459
   Month: 25    P(Cross) if HR=1   0.0060
             P(Cross) if HR=0.73   0.5603
       Final                   Z   1.9930
      N: 492         p (1-sided)   0.0231
 Events: 441        ~HR at bound   0.8270
   Month: 60    P(Cross) if HR=1   0.0250
             P(Cross) if HR=0.73   0.9000



Cross-check, upper boundaries: gsDesign 3.71, 2.511, 1.993 | rpact 3.71, 2.511, 1.993

15. Analyses Reported by the Sponsor

The registry record reports the sponsor’s primary comparisons as hazard ratios from Wald-type tests. For the 28-day ciprofloxacin schedule versus pooled placebo, the reported hazard ratio was 0.733, the 97.5% confidence interval was 0.503 to 1.069, and the p-value was 0.065. For the 14-day schedule versus pooled placebo, the reported hazard ratio was 0.533, the 97.5% confidence interval was 0.357 to 0.797, and the p-value was 0.001.

Those reported analyses are the relevant results for the primary endpoint. There is no discrepancy flag for the primary comparisons. The continuous-outcome comparisons described as recalculated are different: they are simple unadjusted recalculations from posted group summaries, and the registry does not list sponsor-reported analyses for those comparisons. They should not be treated as equivalent to a trial-specific adjusted analysis.

A recalculation from summary means and standard deviations cannot reproduce methods that may have used participant-level measurements, covariate adjustment, repeated measures, or specific missing-data assumptions. Details of any such sponsor methods for the continuous outcomes are not reported in the registry record. Accordingly, the sponsor’s own reported analysis takes precedence wherever it is available; recalculated results serve only as an approximate descriptive comparison where no sponsor analysis is posted.

16. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study tests more than one outcome, comparison, or analysis. Even if each individual test uses a conventional threshold, conducting many tests increases the chance that at least one result will appear notable by chance. This trial has two primary comparisons against pooled placebo and lists multiple secondary outcomes, including exacerbation-related, pathogen, symptom, quality-of-life, and lung-function measures.

The sponsor-reported primary analyses use a 97.5% confidence interval and a Wald-type test. The registry record does not report the rationale for that confidence level, whether the two primary comparisons were handled under a formal multiplicity procedure, or whether any hierarchy or gatekeeping strategy was used. It also does not report a multiplicity adjustment for secondary outcomes. Therefore, the two primary results can be described as posted, but the record does not establish how the family of comparisons was controlled statistically.

Missing-data methods are also not reported in enough detail to reconstruct the analyses. The primary analysis population is identified as the full analysis set of randomized participants, but the registry record does not describe how incomplete follow-up, missing endpoint data, withdrawals, or censoring were handled. For the secondary continuous outcomes, the numbers contributing to the posted summaries are smaller than the randomized group counts, and the reason for each difference is not reported in the registry record. It is not possible to determine from the posted results alone whether these differences reflect missing measurements, the outcome-specific analysis population, or another reason.

These omissions matter because the way missing observations and multiple comparisons are handled can affect estimates, uncertainty, and interpretation. The registry record does not report the trial’s full statistical analysis plan, interim analyses, or sensitivity analyses. No particular procedure should be assumed. Results from secondary outcomes and comparisons should consequently be read with appropriate caution, and the confidence intervals should be understood as conditional on the method used rather than as a complete account of all uncertainty.

17. 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: bronchiectasis (12.4%), pneumonia (3.6%), cardiac failure (1.5%), haemoptysis (1.5%), infective exacerbation of bronchiectasis (1.4%).

The registry reports serious adverse events in 29 of 141 participants in the 28-day ciprofloxacin group, 23 of 136 in the 14-day ciprofloxacin group, and 32 of 137 in pooled placebo. Other adverse events are reported for 74 of 141, 83 of 136, and 62 of 137 participants, respectively. These are participant counts in the safety groups, not event rates calculated. The safety denominators differ from some of the primary endpoint group counts.

The most frequent listed serious adverse-event terms include bronchiectasis at 12.4%, pneumonia at 3.6%, cardiac failure at 1.5%, haemoptysis at 1.5%, infective exacerbation of bronchiectasis at 1.4%, and atrial fibrillation at 0.7%. These terms describe reported events and do not establish that study treatment caused them. The registry record does not report deaths in the posted safety summary.

Counts of participants with adverse events do not by themselves show event severity beyond the serious-event classification, timing, duration, or whether a participant had more than one event. A comparison of these counts also does not establish a causal difference. The safety findings should be read as descriptive information within the trial, with the limitations of the posted summary.

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

The primary results describe the timing of a first qualifying pulmonary exacerbation during up to 48 weeks of follow-up. The sponsor-reported comparison for the 14-day intermittent schedule had a hazard-ratio confidence interval below 1, while the interval for the 28-day schedule included 1. This is a statistical description of the posted analyses, not a complete account of individual experiences or a direct comparison between the two active schedules.

A hazard ratio is a relative measure. It does not state the absolute probability that a participant will experience an exacerbation by a particular date, and it does not mean that every participant’s event time changes by the same amount. Median time estimates offer a separate time-scale description, but some median values or limits are not reported in the registry record. The primary endpoint also counts only the first qualifying event, so it cannot describe the full burden of recurrent exacerbations.

The secondary outcomes provide other perspectives, but their unadjusted recalculations and incomplete reporting mean they should not be treated as a single confirmatory body of evidence. A difference in event timing does not automatically imply a corresponding change in symptoms, quality of life, lung function, pathogen status, or safety. Those outcomes require their own estimates and careful interpretation.

The findings do not establish that one schedule is superior to the other, because the posted primary analyses compare each schedule with pooled placebo rather than directly with one another. They also do not settle the effects beyond the study’s follow-up or in populations not described by the record. The registry record does not report enough information about missing data, multiplicity, or the original analysis plan to evaluate every aspect of robustness. The appropriate reading is limited to the comparisons, outcome definitions, follow-up, and uncertainty reported in the record.

19. Why This Trial Matters Statistically

This trial illustrates why the endpoint and effect measure matter. A time-to-first-event analysis uses the timing of an event and accounts for follow-up duration, while a simple event proportion would not capture when the first exacerbation occurred. The hazard ratio and median time are complementary summaries, but they answer different questions and should not be treated as interchangeable.

It also illustrates the importance of defining a clinically qualifying event. Here, the primary event required systemic antibiotic use, specified general symptoms, and worsening of at least three signs or symptoms. The result therefore concerns events meeting that definition, rather than every respiratory change or exacerbation label used in ordinary clinical practice.

The two schedules were assessed against pooled placebo, and the primary estimates differ in precision and in whether their confidence intervals include the null value. This makes clear why a point estimate alone is inadequate: an estimate must be read alongside its uncertainty and the analysis method. The posted medians also demonstrate that incomplete confidence limits can constrain interpretation even when a point estimate is available.

Finally, the record distinguishes sponsor-reported primary analyses from recalculated secondary comparisons. That distinction is important in biostatistics education: summary-statistic calculations can help readers understand scale and uncertainty, but they cannot reproduce a prespecified analysis based on participant-level data. The unreported elements—such as the original sample-size justification, multiplicity strategy, and missing-data procedures—also show why registry results are informative but do not necessarily contain every detail needed for a full statistical audit.

20. 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 limitations specific to this record constrain interpretation. The primary median time is incomplete for both active schedules: the 28-day group has no reported upper confidence limit, while the 14-day group has no reported median estimate or upper confidence limit. The result is therefore more fully represented by the sponsor-reported hazard ratios than by complete median estimates and intervals.

The primary comparisons are each against pooled placebo. The posted results do not report a direct comparison between the two ciprofloxacin schedules, so their hazard-ratio estimates cannot be used as a formal test of which schedule differs more from the other. The registry also does not report how the pooled placebo groups were constructed analytically or whether any schedule-specific placebo comparison was planned for the primary endpoint.

The registry record does not report the original sample-size justification, detailed statistical analysis plan, multiplicity procedure, interim analyses, or sufficient missing-data and censoring details to reconstruct the analysis. It also does not report results for every listed secondary outcome in the summaries. These are reporting limitations; they do not establish that the procedures or results were absent from other trial documents.

The continuous-outcome comparisons are recalculated from group summaries and do not reproduce a sponsor analysis. Their participant counts vary by outcome and are smaller than the primary analysis counts, with reasons not reported in the registry record. Safety counts use their own denominators, which differ slightly from the primary endpoint counts. These distinct analysis populations should not be combined. Finally, the registry’s description of the study population and setting is limited, restricting assessment of how well the results may apply beyond the enrolled participants.

21. Related Tutorials

22. Related Statistical Calculators

23. Sources

• ClinicalTrials.gov: Ciprofloxacin Dry Powder for Inhalation in Non-cystic Fibrosis Bronchiectasis (Non-CF BE) — NCT01764841.
• Registry record last updated 2018-01-24; status last verified 2018-01.
• Results first posted 2017-05-24.
• 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.

24. Record Summary

The registry record describes a completed, randomized, quadruple-masked, parallel-group phase 3 trial of intermittent ciprofloxacin dry powder for inhalation in non-cystic fibrosis bronchiectasis. It enrolled 416 participants and compared 28-day on/off and 14-day on/off ciprofloxacin schedules with pooled placebo over a 48-week treatment phase.

The primary outcome was time to first qualifying pulmonary exacerbation. The sponsor-reported hazard ratio was 0.733 for the 28-day schedule versus pooled placebo, with a 97.5% confidence interval from 0.503 to 1.069 and p = 0.065. For the 14-day schedule, the reported hazard ratio was 0.533, with a 97.5% confidence interval from 0.357 to 0.797 and p < 0.001. The registry also posts selected secondary and safety results, but key details of multiplicity, missing-data handling, and the original sample-size justification are not reported in the registry record.