A Clinical Study to Test How Effective and Safe GLPG1690 is for Participants With Idiopathic Pulmonary Fibrosis (IPF) When Used Together With Standard of Care: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Clinical Study to Test How Effective and Safe GLPG1690 is for Participants With Idiopathic Pulmonary Fibrosis (IPF) When Used Together With Standard of Care (NCT03733444), a randomized phase 3 study. The primary outcome is Annual Rate of Decline in Forced Vital Capacity (FVC) up to Week 52.

2. Clinical Question

3. Trial Design

This was a phase 3, randomized, double-blind, parallel-group, placebo-controlled, multicenter study. The registry describes masking as quadruple. Participants were assigned to GLPG1690 600 mg, GLPG1690 200 mg, or matching placebo, with local standard of care used alongside the assigned study tablets. The study title specifies a minimum treatment period of 52 weeks. Mean treatment duration was 332.9 days for 600 mg, 336.9 days for 200 mg, and 346.2 days for placebo.

The trial enrolled 781 participants and is listed as terminated. The registry records a start date of 2018-11-05 and a primary completion date of 2021-03-30. The reported primary analysis used the Full Analysis Set. The registry record does not report the reason for termination, the original recruitment target, or whether the termination altered the planned analyses.

Both active groups and placebo groups were managed with local standard of care. The record identifies pirfenidone or nintedanib at a stable dose, or neither, as possible background-care arrangements. It does not report how many participants were receiving each background treatment in the posted results, nor does it provide subgroup estimates by background treatment.

Random allocation and masking are design features intended to reduce systematic differences in treatment assignment and outcome assessment. They do not, by themselves, establish that all sources of bias were eliminated. The registry record does not report the allocation ratio, the randomization procedure, the identities of the parties included in quadruple masking, or further details of site procedures.

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 1431 participants were screened for the study, and 781 were randomized and 777 were treated.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full Analysis Set

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

Population: Full analysis set (FAS) consisted of all randomized participants who received at least 1 dose of investigation product (IP).

6. Primary Endpoint

The registry lists the primary outcome as Annual Rate of Decline in Forced Vital Capacity (FVC) up to Week 52, measured over Baseline up to week 52.

The primary endpoint was the annual rate of decline in forced vital capacity (FVC) from baseline up to week 52, measured in mL/year. FVC is the maximum amount of air a participant can exhale after taking the deepest possible breath, as measured by spirometry. The endpoint is continuous: it describes the estimated amount of lung volume change over time rather than simply classifying each participant as having or not having an event.

Annualizing the change expresses the rate on a common time scale, while the baseline-to-week-52 timeframe focuses the primary comparison on the first year of follow-up. A negative rate indicates decline. The trial reports least-squares means for each group and least-squares mean differences between each GLPG1690 dose and placebo. These are model-based estimates, not simple counts of participants with progression.

FVC is used in this study as a measure of lung function. A group contrast estimates how the average rate differed between assigned groups under the analysis model. The contrast alone does not show the distribution of individual participant outcomes, and it does not describe every aspect of IPF or overall health. The registry identifies the primary population as the Full Analysis Set. Further endpoint details, including the model covariates and the handling of measurements not available at scheduled visits, are not reported in the registry record.

7. Results Posted in the Registry

• GLPG1690, 600 mg: mean -173.80 versus -176.60 on control; difference 2.80 (95% CI -46.79 to 52.39), standardized effect d = 0.01; z-test p = 0.912.
• GLPG1690, 200 mg: mean -174.90 versus -176.60 on control; difference 1.70 (95% CI -47.35 to 50.75), standardized effect d = 0.01; z-test p = 0.946.

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.

Percentage of Participants With Disease Progression Up to 52 Weeks

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • GLPG1690, 600 mg: 23.9% (62/259) versus 22.1% (57/258) on control; risk difference 1.8 percentage points (95% CI -5.4 to 9.1), risk ratio 1.08 (0.79–1.49); unadjusted two-proportion z-test p = 0.618.
  • GLPG1690, 200 mg: 23.1% (60/260) versus 22.1% (57/258) on control; risk difference 1.0 percentage points (95% CI -6.2 to 8.2), risk ratio 1.04 (0.76–1.44); unadjusted two-proportion z-test p = 0.789.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between GLPG1690, 600 mg 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 GLPG1690, 200 mg and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Participants With Respiratory-Related Hospitalization Until End of Study (EoS)

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • GLPG1690, 600 mg: 13.5% (35/259) versus 6.6% (17/258) on control; risk difference 6.9 percentage points (95% CI 1.8 to 12.1), risk ratio 2.05 (1.18–3.57); unadjusted two-proportion z-test p = 0.009.
  • GLPG1690, 200 mg: 10.8% (28/260) versus 6.6% (17/258) on control; risk difference 4.2 percentage points (95% CI -0.7 to 9.0), risk ratio 1.63 (0.92–2.91); unadjusted two-proportion z-test p = 0.091.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for GLPG1690, 600 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between GLPG1690, 200 mg and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline in St.George's Respiratory Questionnaire (SGRQ) Total Score at Week 52

• 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:
  • GLPG1690, 600 mg: mean 4.60 versus 4.70 on control; difference -0.10 (95% CI -3.19 to 2.99), standardized effect d = -0.01; z-test p = 0.949.
  • GLPG1690, 200 mg: mean 4.30 versus 4.70 on control; difference -0.40 (95% CI -3.42 to 2.62), standardized effect d = -0.02; z-test p = 0.795.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between GLPG1690, 600 mg 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 GLPG1690, 200 mg and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes span disease progression, respiratory-related hospitalization, FVC decline over longer follow-up, SGRQ scores, all-cause hospitalization, and respiratory-related mortality. These outcomes provide additional perspectives on disease course and participant experience, but they do not replace the prespecified primary FVC comparison. Across the reported secondary findings, the pattern is not a consistent signal of improvement across outcome types: estimates vary by endpoint and dose, and some comparisons are imprecise.

Some posted comparisons for respiratory-related hospitalization point toward more events in the GLPG1690 groups than placebo, while the disease-progression and SGRQ comparisons do not show a clear separation from placebo. These are descriptive observations from separate endpoints, not a unified conclusion about treatment effect. Further secondary endpoint estimates and analysis details are not reported in the registry record, so the full pattern cannot be independently assessed from the information available.

General: Secondary analyses are often numerous and may involve different definitions, timeframes, populations, and statistical models. Unless the testing sequence and multiplicity adjustment are known, an isolated unadjusted result carries less evidential weight than a primary result specified to address the main study question. Repeated testing increases the chance of findings that appear notable by chance. Secondary outcomes can support context and generate questions, but they should be interpreted with attention to their confidence intervals, event counts, and the broader testing strategy.

The primary estimate itself is imprecise and close to no difference. Secondary findings that point in different directions do not resolve that uncertainty. The registry record does not report a complete multiplicity strategy or the full statistical analysis plan, so the secondary analyses should be viewed as supportive or exploratory rather than as independent confirmation of a treatment effect.

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

• Percentage of Participants With Disease Progression Up to 52 Weeks
• Percentage of Participants With Respiratory-Related Hospitalization Until End of Study (EoS)
• Change From Baseline in St.George's Respiratory Questionnaire (SGRQ) Total Score at Week 52
• Annual Rate of Decline of FVC Until EoS
• Percentage of Participants With Disease Progression Until EoS
• Change From Baseline in St. George's Respiratory Questionnaire (SGRQ) Total Score at Week 100
• Percentage of Participants With All Cause Hospitalization Until EoS
• Percentage of Participants With Respiratory Related Mortality Until EoS

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous, so the central summary is a mean rate for each group and a mean difference comparing each GLPG1690 dose with placebo. The sponsor reports least-squares means and least-squares mean differences from a Coefficient Regression Model. A least-squares mean is a model-based group estimate. The registry record does not report the full model specification, including its covariates, assumptions, or detailed treatment of repeated measurements.

General: A mean difference expresses the estimated contrast on the outcome's original scale. For this trial, that scale is mL/year. A positive contrast means the estimated rate in the active group is numerically higher, or less negative, than the placebo estimate. It does not establish that this difference is reliable or clinically important; uncertainty and the analysis model also matter.

The registry reports standard errors alongside group least-squares means. A standard error describes uncertainty in an estimated mean, rather than the spread of individual participant measurements. The unadjusted recalculations use the posted standard errors to approximate a pooled standard deviation and a standardized effect. Because those inputs are summary statistics rather than individual participant data, the recalculated standard deviations are approximate. The recalculated contrasts are simple, unadjusted comparisons and do not reproduce the sponsor's regression model.

General: A confidence interval is a range of values compatible with the estimate and the method's assumptions. A wider interval indicates less precision. An interval that includes the no-difference value does not demonstrate that the true effect is exactly absent; it indicates that the data and method do not rule out that value at the stated confidence level. A p-value measures how incompatible the observed data are with a specified null hypothesis under the analysis assumptions. It is not the probability that the null hypothesis is true.

The sponsor reports superiority analyses for each dose against placebo. The primary contrasts have p-values of 0.912 and 0.946, respectively, and their 95% confidence intervals include the no-difference value. The recalculated unadjusted p-values are 0.912 and 0.946. Small differences in the printed limits and p-values reflect that the registry-reported analyses use a regression model, whereas the recalculations use posted group summaries and are approximate.

The secondary outcomes include binary outcomes, continuous questionnaire scores, and time-to-event outcomes. These require different summaries. A risk difference compares the observed proportions between groups. An odds ratio compares the odds of an event, while a hazard ratio compares event rates over time under a time-to-event analysis. A least-squares mean difference for a questionnaire score remains a contrast on that score's scale. These measures answer related but not identical questions, so their values should not be treated as if they were interchangeable.

General: For binary outcomes, an estimate based on a small number of events can be imprecise, and a percentage alone does not convey that uncertainty. For time-to-event outcomes, the timing of events and the duration of observation contribute to the analysis. A hazard ratio is not the same as a risk difference or a ratio of the final percentages. The registry record does not report all model details for the posted secondary analyses, so interpretation should remain tied to the reported measure and its interval.

Multiplicity arises when many endpoints, doses, timepoints, or statistical comparisons are examined. General: When many hypotheses are tested, the chance of at least one apparently notable result can increase unless the testing strategy accounts for the number and ordering of comparisons. The registry record does not report whether a multiplicity adjustment or hierarchical testing procedure was used for the full set of outcomes. The recalculated p-values are unadjusted, and they should not be treated as a complete substitute for the sponsor's prespecified analysis strategy.

The registry lists 35 outcome measures and 26 analyses. It identifies the Full Analysis Set for the primary outcome, but does not report enough detail to reconstruct every analysis population or all analysis decisions. Interim analyses, the full statistical analysis plan, and the study's original sample-size justification are not reported in the registry record. Those gaps limit independent assessment of the intended testing sequence, missing-data procedures, and any adaptations made during the trial.

11. Confidence Intervals and Precision

The sponsor-reported primary 95% confidence interval is -46.9 to 52.4 mL/year for GLPG1690 600 mg versus placebo, and -47.4 to 50.8 mL/year for 200 mg versus placebo. Each interval spans values below and above the no-difference value. Thus, the point estimates are not precise enough to determine whether either dose was associated with a lower or higher annual FVC decline than placebo.

General: A confidence interval communicates the uncertainty around an estimate under the analysis method. It is not a range containing a fixed proportion of individual participant outcomes, and it does not assign probabilities to particular values after the data have been observed. Its width depends on factors such as variability, sample size, and the statistical model. A narrow interval is more informative about the size and direction of a contrast than a wide interval.

The recalculated intervals are -46.79 to 52.39 mL/year for 600 mg and -47.35 to 50.75 mL/year for 200 mg. They are close to the sponsor's model-based limits, with small differences in rounding and method. Because the recalculations are unadjusted and approximate, the sponsor's reported intervals are the main reference for the trial's formal analysis.

The group estimates are based on 259 participants in the 600 mg group, 260 in the 200 mg group, and 258 in the placebo group. Those group sizes should be considered alongside the broad intervals: the issue is not simply whether a result has a small p-value, but how much the data constrain plausible differences. The posted primary results remain compatible with a range of effects in either direction. They do not provide a precise estimate of a small treatment contrast.

12. Planning a Similar Trial: Sample Size

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

The planning illustrations are per arm for the continuous primary outcome; they are not total-event counts. The 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 original trial's own design assumptions and sample-size justification are not reported in the registry record.

For example, planning to detect 100% of the observed 600 mg contrast gives 165,678 participants per arm for 80% power and 221,796 participants per arm for 90% power. The corresponding illustration for 200 mg gives 440,487 participants per arm for 80% power and 589,687 participants per arm for 90% power. These very large illustrations reflect the small observed contrasts relative to the estimated variability; they are not proposed enrollment targets for a future study.

General: The 80% power column gives the calculated group size under the stated assumptions for an 80% chance of detecting the chosen effect at the specified significance level, if that effect and assumptions were true. The 90% power column gives the analogous size for a higher chance of detection. Higher power generally requires more participants when other assumptions are held constant. Planning for a smaller effect also requires more participants, because a smaller contrast is harder to distinguish from random variation.

These figures are planning illustrations based on the observed effect, not observed power. They should not be read as an assessment of the probability that the completed trial succeeded, or as evidence about whether the study was adequately designed. The trial's original assumptions are not reported in the registry record, and an observed effect can be an unstable basis for planning when the estimate is imprecise.

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 = 2.800; pooled standard deviation σ = 287.654.
2. n = 2 × (1.96 + 0.842)² × 287.654² / 2.800² = 165,677.4, rounded up to 165,678 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 <- 2.79999999999998                      # observed difference in means
sigma <- 287.654258222259                     # 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(3733444)
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 = 165,678 (80% power), 221,796 (90% power)
 75% of observed effect: n per arm = 294,538 (80% power), 394,303 (90% power)
 50% of observed effect: n per arm = 662,710 (80% power), 887,181 (90% power)
power.t.test: 165678.3 
Simulated power at n = 165,678 per arm: 0.800 (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 analysis uses a Coefficient Regression Model and reports least-squares mean differences. For GLPG1690 600 mg versus placebo, it gives a difference of 2.8 mL/year, a 95% confidence interval from -46.9 to 52.4, and p = 0.912. For 200 mg versus placebo, it gives 1.7 mL/year, a 95% confidence interval from -47.4 to 50.8, and p = 0.946.

The unadjusted recalculations from the posted summary statistics give the same point estimates after rounding, with slightly different interval limits and p-values. They approximate a two-group comparison and do not account for the sponsor's regression model. The standard deviations used in those calculations are reconstructed from the reported standard errors, which adds approximation. The sponsor's analysis is therefore the appropriate primary reference for the trial's reported statistical results; recalculations serve as a check on scale and broad interpretation, not as a replacement.

Both approaches indicate that the primary estimates are close to no difference and that the intervals are broad. The distinction between them matters because model-based analyses may use information and adjustments not recoverable from aggregate summaries. Covariates and other model details are not reported in the registry record, so the sponsor's analysis cannot be fully reproduced from the posted group summaries alone.

15. Multiplicity, Missing Data and Analysis Populations

The registry record identifies the primary outcome and reports multiple secondary outcomes and analyses, but a complete statistical analysis plan is not reported in the registry record. In particular, the record does not report whether the sponsor used a formal multiplicity adjustment, a hierarchical testing sequence, or another procedure to control error across doses, endpoints, or timepoints. The unadjusted recalculated p-values therefore cannot be interpreted as if they were adjusted for all the analyses conducted.

Missing-data procedures are also not reported in enough detail to assess how unavailable FVC measurements or other outcome data were handled. The registry identifies the Full Analysis Set for the primary outcome, but the membership rules and analysis populations for all other outcomes are not reported in the registry record. The record does not provide the amount or pattern of missing data, reasons for missingness, or sensitivity analyses addressing alternative assumptions.

Interim analyses and any related decision rules are not reported in the registry record. Neither the rationale for termination nor whether it affected follow-up or analysis is reported. Without this information, it is not possible to determine from the registry record whether the outcome reporting followed the originally intended schedule or testing strategy.

General: Multiplicity matters because testing many hypotheses can increase the chance of a false-positive finding if the analysis does not account for that testing. Missing data matter because the observed participants may not represent all randomized participants if availability depends on outcomes or other factors. Sensitivity analyses can show how conclusions change under different assumptions, but their presence and results are not reported. These omissions do not establish that the analyses were inappropriate; they limit what can be assessed independently from the registry record.

16. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Deaths

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: idiopathic pulmonary fibrosis (7.7%), respiratory failure (2.7%), pneumonia (2.3%), covid-19 (1.5%), acute myocardial infarction (0.8%).

The serious adverse event figures report 42 affected participants among 258 at risk in the placebo group, 64 among 259 at risk in the GLPG1690 600 mg group, and 63 among 260 at risk in the 200 mg group. The figures for participants affected by other adverse events are 117 of 258, 141 of 259, and 134 of 260, respectively. Death counts were 12, 23, and 21 in those same groups.

The registry also lists serious-event terms with percentages: idiopathic pulmonary fibrosis, 7.7%; respiratory failure, 2.7%; pneumonia, 2.3%; COVID-19, 1.5%; acute myocardial infarction, 0.8%; and myocardial infarction, 0.8%. The posted percentages describe the listed terms; the registry record does not report further details about attribution or overlap between terms.

These counts describe events recorded in each group and are not, by themselves, evidence that the study drug caused an event or that group differences are statistically reliable. They also do not summarize event timing, duration, severity beyond the serious-event classification, or all clinical circumstances. The registry record does not report enough information to make a causal comparison from these counts alone.

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

The primary result describes estimated annual FVC decline through week 52 in the Full Analysis Set. The GLPG1690 group estimates were numerically close to the placebo estimate, and the sponsor-reported dose-versus-placebo differences had broad 95% confidence intervals that included the no-difference value. The data therefore do not establish a clear difference in the primary outcome between either dose and placebo.

This does not prove that the true effects were exactly zero, nor does it show that all possible effects can be ruled out. The intervals remain compatible with differences in either direction. The estimate for each dose is an average group contrast under the sponsor's model; it does not predict an individual participant's outcome or describe every aspect of IPF.

The secondary outcomes and safety counts add context but do not turn the primary estimate into a precise or definitive conclusion. Secondary comparisons involve varied outcome types and may be subject to multiplicity. Safety event counts are descriptive and do not, without additional analysis and context, establish causation. The record does not report the full analysis plan, missing-data procedures, or multiplicity strategy needed for a complete independent assessment.

The study is listed as terminated. The reason for termination and its implications for the study's conduct are not reported in the registry record. The posted results should therefore be read as the estimates from the reported analyses and follow-up, not as a complete account of every design decision or source of uncertainty. No treatment recommendation follows from these statistical results.

18. Why This Trial Matters Statistically

This trial illustrates why a point estimate should not be interpreted without its uncertainty. The primary estimates for both doses were close to the placebo estimate, while the confidence intervals were wide enough to include potentially meaningful differences in either direction. The central statistical message is therefore about limited precision, not simply about whether the point estimate is positive or negative.

It also highlights the distinction between a sponsor's model-based analysis and an unadjusted recalculation from summary statistics. The recalculations are close to the reported primary contrasts, but they do not reproduce the regression model and use approximate variability estimates. This makes them useful as a transparent cross-check, while leaving the sponsor's analysis as the formal reported result.

Finally, the trial has many outcomes and analyses, including continuous, binary, and time-to-event measures. Their interpretations depend on the analysis method, uncertainty, event frequency, and the overall testing strategy. When multiplicity and missing-data procedures are not reported in enough detail, secondary findings require particular caution. Together, these features show why transparent reporting of model details, analysis populations, missingness, and testing plans is important for interpreting clinical trial results.

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 primary confidence intervals are broad, leaving substantial uncertainty about the size and direction of each dose contrast. The primary group summaries do not show individual participant distributions, and the registry record does not report the full regression model or its covariates. This limits independent evaluation of how the reported estimates were obtained.

The recalculations are unadjusted and approximate. They use standard errors to reconstruct variability and cannot account for any model features not included in the posted aggregate data. They should not be mistaken for a reanalysis of participant-level data.

The trial is listed as terminated, but the reason for termination and any consequences for planned follow-up or analysis are not reported in the registry record. The original sample-size justification, interim analyses, missing-data methods, and full multiplicity strategy are also not reported. These omissions make it difficult to assess whether the posted analyses match the original plan or how robust results are to alternative assumptions.

Only selected secondary outcomes have detailed estimates in the record, while the registry lists 35 outcome measures and 26 analyses. The population and analysis details for all secondary outcomes are not reported. Safety counts also lack causal attribution and detailed context in the posted information, so they should be read descriptively. The study's local standard-of-care arrangements include different background-treatment possibilities, but subgroup results by background treatment are not reported.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Clinical Study to Test How Effective and Safe GLPG1690 is for Participants With Idiopathic Pulmonary Fibrosis (IPF) When Used Together With Standard of Care — NCT03733444.
• Registry record last updated 2022-07-29; status last verified 2022-07.
• Results first posted 2022-07-29.
• 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

NCT03733444 is a randomized, double-blind, parallel-group, placebo-controlled, multicenter phase 3 study in idiopathic pulmonary fibrosis. It compared GLPG1690 600 mg and 200 mg with matching placebo, alongside local standard of care. Enrollment was 781, and the study is listed as terminated.

The primary endpoint was annual FVC decline from baseline to week 52. The sponsor-reported mean differences versus placebo were 2.8 mL/year for 600 mg and 1.7 mL/year for 200 mg; both 95% confidence intervals included the no-difference value. The posted estimates are close to placebo and imprecise. Secondary outcomes and adverse-event counts provide additional context, but important details about multiplicity, missing data, and the full analysis plan are not reported in the registry record.