A Clinical Study to Test How Effective and Safe GLPG1690 is for Subjects 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 Subjects With Idiopathic Pulmonary Fibrosis (IPF) When Used Together With Standard of Care (NCT03711162), a randomized phase 3 study. The primary outcome is Annual Rate of Decline in FVC up to Week 52.

2. Clinical Question

3. Trial Design

This was a phase 3, randomized, parallel-group, placebo-controlled, multicenter trial. The official title describes it as double-blind, while the registry design information records quadruple masking. Participants were assigned to GLPG1690 600 mg, GLPG1690 200 mg, or matching placebo, with local standard of care in each group. The registry identifies pirfenidone or nintedanib as standard-care options and says these were to be at a stable dose for at least 2 months before screening.

The study was intended to evaluate efficacy and safety for a minimum of 52 weeks. The primary efficacy outcome was the annual rate of decline in FVC up to week 52. Other listed outcomes included disease progression, respiratory-related hospitalization, change in St. George's Respiratory Questionnaire total score, FVC decline through the end of the study, all-cause hospitalization, and respiratory-related mortality. The record lists 35 outcome measures and 26 analyses.

The registry reports 525 participants enrolled, and the primary efficacy analysis set included randomized participants who received at least 1 dose, subject to the stated site-level exclusion for serious good clinical practice noncompliance. The analysis counts shown for the primary outcome are 169 for GLPG1690 600 mg, 171 for GLPG1690 200 mg, and 164 for placebo. These counts describe the outcome analysis groups, not the full enrollment.

The study status is terminated. The registry lists a start date of 2018-11-28 and a primary completion date of 2021-03-30. The reason for termination and any consequences for follow-up are not reported in the registry record. The original design assumptions, including the planned sample-size justification and any interim analysis arrangements, are also not reported in the registry record.

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 1116 participants were screened for the study, and 525 were randomized and 523 were treated.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full Analysis Set - Efficacy (FAS-EF) included all randomized participants who received at least 1 dose of investigational product and excluded participants from the site found to have serious good clinical practice (GCP)-noncompliance issues.

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 investigational product (IP).

6. Primary Endpoint

The registry lists the primary outcome as Annual Rate of Decline in 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 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. An annualized rate expresses change over time on a common yearly scale, allowing the trial to compare the course of lung-function measurements between randomized groups over the follow-up period.

The registry reports least-squares means for this endpoint and standard errors as their dispersion measure. The posted mean estimates are negative in all three groups, representing decline on the endpoint's scale. The comparison of interest is the difference between each GLPG1690 dose group and placebo, not whether a single group’s estimate is numerically above or below zero. The estimated difference and its confidence interval describe both the direction and uncertainty of the between-group contrast.

FVC is used as a measurable lung-function outcome in this trial; the registry states its measurement definition but does not report a rationale for selecting it as the primary endpoint. A result on FVC alone does not summarize every aspect of IPF or every outcome that matters to participants. The trial also included patient-reported, disease-progression, hospitalization, and mortality outcomes, but those are distinct measures and should not be treated as interchangeable with the primary FVC endpoint.

7. Results Posted in the Registry

• GLPG1690 600 mg: mean -124.60 versus -147.30 on control; difference 22.70 (95% CI -51.96 to 97.36), standardized effect d = 0.07; z-test p = 0.551.
• GLPG1690 200 mg: mean -173.90 versus -147.30 on control; difference -26.60 (95% CI -100.10 to 46.90), standardized effect d = -0.08; z-test p = 0.478.

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 Week 52

• 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: 17.8% (30/169) versus 18.3% (30/164) on control; risk difference -0.5 percentage points (95% CI -8.8 to 7.7), risk ratio 0.97 (0.61–1.53); unadjusted two-proportion z-test p = 0.898.
  • GLPG1690 200 mg: 18.7% (32/171) versus 18.3% (30/164) on control; risk difference 0.4 percentage points (95% CI -7.9 to 8.7), risk ratio 1.02 (0.65–1.60); unadjusted two-proportion z-test p = 0.921.
• 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: 9.5% (16/169) versus 9.8% (16/164) on control; risk difference -0.3 percentage points (95% CI -6.6 to 6.0), risk ratio 0.97 (0.50–1.88); unadjusted two-proportion z-test p = 0.929.
  • GLPG1690 200 mg: 9.4% (16/171) versus 9.8% (16/164) on control; risk difference -0.4 percentage points (95% CI -6.7 to 5.9), risk ratio 0.96 (0.50–1.85); unadjusted two-proportion z-test p = 0.901.
• 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.

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 3.30 versus 3.80 on control; difference -0.50 (95% CI -4.34 to 3.34), standardized effect d = -0.03; z-test p = 0.799.
  • GLPG1690 200 mg: mean 4.10 versus 3.80 on control; difference 0.30 (95% CI -3.41 to 4.01), standardized effect d = 0.02; z-test p = 0.874.
• 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 registry lists a broad set of secondary outcomes covering disease progression, hospitalizations, questionnaire scores, FVC over longer follow-up, and mortality. The posted numerical comparisons available for these outcomes show a generally similar interpretive pattern to the primary endpoint: the point estimates do not form a consistent, clearly separated pattern across both GLPG1690 doses, and the reported uncertainty includes values compatible with no difference for the comparisons described. This broad observation does not mean all outcomes are identical or that one endpoint can stand in for another.

The secondary measures address different questions. Progression is a binary outcome in the posted analysis, hospitalization is an event occurring over follow-up, and SGRQ is a questionnaire score. The registry also lists later follow-up outcomes, including FVC decline and mortality. These outcomes have different scales and analysis methods, so their estimates cannot be combined into one summary effect by simply comparing their numerical values. Nor do secondary results substitute for the primary FVC analysis.

Unadjusted secondary results generally carry less inferential weight when many outcomes and comparisons are examined. As a general statistical principle, making numerous tests raises the chance that at least one result appears notable by chance, even when no underlying difference exists. Adjustment procedures can address multiplicity, but the registry’s plan for handling multiple comparisons across outcomes is not reported in the registry record. Accordingly, individual unadjusted secondary p values should be treated as exploratory evidence, not as stand-alone confirmation.

The record lists 35 outcome measures and 26 analyses, while the secondary outcomes include distinct follow-up periods and endpoints. The broad pattern can contextualize the primary result, but the secondary evidence does not resolve the uncertainty in the primary comparison. Details of missing observations, analysis populations for each secondary outcome, and any prespecified hierarchy are not reported in the registry record.

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

• Percentage of Participants With Disease Progression up to Week 52
• 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 in 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 endpoint is continuous: it is measured on a numeric scale in mL/year. The registry reports a least-squares mean for each group and a least-squares mean difference for each dose compared with placebo. A least-squares mean is a model-based group estimate. It can differ from a simple arithmetic average because it comes from a statistical model; the registry names a Coefficient Regression Model for the primary comparisons but does not report the full model specification or its covariates.

What does the standard error describe?

A standard error describes the statistical uncertainty in an estimated mean. It is not the spread of individual participants’ measurements. The primary group results report standard errors of 27.15 for GLPG1690 600 mg, 26.31 for GLPG1690 200 mg, and 26.72 for placebo. These values indicate uncertainty around the group estimates, while individual FVC outcomes may vary more widely. The registry does not provide participant-level data in the record, so individual outcome distributions cannot be reconstructed from these summary measures alone.

How should a mean difference be read?

A mean difference compares the estimated outcome in one treatment group with the estimated outcome in the reference group. For the primary endpoint, positive differences indicate a higher estimated annual rate than placebo on the reported scale, while negative differences indicate a lower estimated rate. The meaning of a direction should be understood in relation to the endpoint definition and the fact that all three group estimates are negative. A difference is not the same thing as either group’s absolute change, and it does not indicate the outcome for any one participant.

What does a confidence interval add?

A confidence interval gives a range of values compatible with the estimated comparison under the analysis assumptions. Its width reflects precision: a wider range leaves more uncertainty about the size and direction of the difference. When the interval includes zero, the data are compatible with no between-group difference as well as with differences on either side of zero. This is not proof that the groups are identical. Intervals depend on the statistical model and data assumptions, and the registry’s reported intervals are the sponsor’s analysis results.

What does a p value tell the reader?

A p value describes how unusual the observed data, or more extreme data, would be under a specified null hypothesis and analysis model. It is not the probability that the null hypothesis is true, and it does not state the probability that a treatment effect exists. The p values reported for the primary comparisons are 0.552 and 0.478. These values do not provide evidence against the no-difference null at conventional thresholds, but they do not show that the treatments are equivalent or that a potentially important difference has been ruled out. The registry’s full inferential plan and any adjustment for multiple comparisons are not reported in the registry record.

Why distinguish the registry analysis from recalculation?

The sponsor-reported primary results use the named Coefficient Regression Model and give least-squares mean differences, confidence intervals, and p values. The recalculated comparisons are simple, unadjusted estimates from the posted group summaries. They use a pooled standard deviation approximated from the reported standard errors, as indicated in the analysis description. This is a different calculation from the sponsor’s model-based analysis, so small discrepancies in estimates or interval endpoints can arise. They are not evidence that the underlying participant-level analyses are identical.

Why can over-dispersion matter?

As a general statistical point, over-dispersion occurs when observed variability is greater than a model assumes. It can make standard errors too small if it is ignored, yielding confidence intervals that are too narrow and p values that appear more decisive than warranted. This concern is especially relevant to outcomes involving counts or binary events when the model’s variance assumptions do not fit the data. The record does not report an over-dispersion assessment for the primary continuous endpoint, and no claim about whether it occurred can be made from the posted summaries.

Other registry analyses use different methods according to endpoint type. For example, the progression outcome reports logistic regression odds ratios, and respiratory-related hospitalization reports hazard ratios. These are not the same estimand as the primary mean difference. General interpretation must account for each outcome’s scale, follow-up period, and method. The registry does not report all model details or the full handling of missing data for these analyses.

11. Confidence Intervals and Precision

The primary confidence intervals are broad relative to their point estimates and cross zero. For the 600 mg comparison, the sponsor reports a 95% interval from -52.3 to 97.6 mL/year around an estimate of 22.7 mL/year. For the 200 mg comparison, the reported 95% interval runs from -100.5 to 47.1 mL/year around an estimate of -26.7 mL/year. Both ranges include no difference and allow for effects in either direction. The interval endpoints, rather than the point estimate alone, show how much uncertainty remains in the between-group comparison.

A confidence interval is not a range containing a known fixed share of individual participant outcomes. It is a measure of uncertainty around an estimated group contrast under the analysis method and its assumptions. A narrower interval would indicate greater precision for that estimate; these intervals leave substantial uncertainty about the size and direction of the difference. They do not establish that any value within the interval is equally likely, and the interval does not capture every source of uncertainty, such as unreported analysis choices or limitations in the registry record.

The recalculated intervals are close to the sponsor’s intervals but are not identical. The recalculations use summary statistics and approximate standard deviations, whereas the sponsor reports model-based least-squares comparisons. For interpretation of the trial result, the sponsor’s own analysis is the principal analysis recorded by the registry. The recalculated estimates are useful as a transparent, unadjusted cross-check, not as a replacement for the sponsor’s analysis.

Precision also depends on the amount and quality of information contributing to an analysis, the variability of the endpoint, and the model. The primary analysis counts differ by group, and the registry reports exclusions from the efficacy set for serious site-level GCP noncompliance. The record does not report detailed missing-data patterns or sensitivity analyses, so the impact of missing outcomes on precision cannot be assessed from the reported information alone.

12. Planning a Similar Trial: Sample Size

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

The planning figures are illustrations based on the observed effect, not the original trial’s design justification. For continuous outcomes such as the primary FVC endpoint, the figures refer to participants per arm. For time-to-event outcomes, the stated convention is total events, not participants per arm. These planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; each planning scenario targets the stated fraction of the observed effect.

The 80% power column describes the number of participants per arm that the illustration estimates would be needed to have an 80% chance of detecting the specified effect under those assumptions, if that effect were the true one. The 90% power column uses a higher probability of detection and therefore gives a larger planning requirement. For the primary 600 mg comparison, the illustration gives 3,683 participants per arm for 80% power and 4,931 for 90% power when planning for 100% of the observed effect. Planning for 75% or 50% of the observed effect gives larger figures. The same pattern applies to the other comparisons: smaller effects need more participants to detect under otherwise unchanged assumptions.

These calculations are not observed power and do not describe the probability that the completed trial detected a real effect. They are conditional planning illustrations derived from the observed estimate. Because an observed effect can be unstable, especially when uncertain, these figures should not be read as a recommendation or as proof that the trial was designed around those assumptions. The registry does not report the trial’s own original sample-size assumptions or justification. A planning curve, if used alongside the figures, should be read as the same relationship between assumed effect size and required sample size, not as an additional observed trial result.

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 = 22.700; pooled standard deviation σ = 347.689.
2. n = 2 × (1.96 + 0.842)² × 347.689² / 22.700² = 3,682.7, rounded up to 3,683 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 <- 22.7                      # observed difference in means
sigma <- 347.689473085194                     # 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(3711162)
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 = 3,683 (80% power), 4,931 (90% power)
 75% of observed effect: n per arm = 6,548 (80% power), 8,765 (90% power)
 50% of observed effect: n per arm = 14,731 (80% power), 19,721 (90% power)
power.t.test: 3683.7 
Simulated power at n = 3,683 per arm: 0.795 (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-reported primary comparisons are model-based least-squares mean differences from a Coefficient Regression Model. For GLPG1690 600 mg versus placebo, the sponsor reports a difference of 22.7 mL/year, a 95% confidence interval from -52.3 to 97.6, and p = 0.552. For GLPG1690 200 mg versus placebo, the sponsor reports -26.7 mL/year, a 95% confidence interval from -100.5 to 47.1, and p = 0.478.

The recalculated unadjusted comparisons are close: 22.7 for the 600 mg dose and -26.6 for the 200 mg dose, with confidence intervals and p values that are also close to the sponsor’s figures. The small differences are consistent with using different calculation approaches: the sponsor reports model-based estimates, while the recalculations use posted summary statistics and approximate pooled standard deviations. The recalculations are not a reproduction of the full regression model.

The registry record does not flag a discrepancy between the reported results and the recalculations. The sponsor’s analyses remain the direct analyses reported for the trial and should take precedence if an inconsistency arises. Neither set of estimates should be read without its confidence interval, and the recalculations do not add participant-level information beyond what the registry reports.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study evaluates multiple outcomes, treatment comparisons, time points, or statistical tests. Each additional test creates another opportunity for a result to look unusual by chance. This trial includes two dose comparisons against placebo and a range of secondary outcomes, so interpreting isolated p values requires knowing whether the analyses were prespecified and whether the testing strategy controlled the overall error rate. The registry does not report a multiplicity adjustment strategy or a formal testing hierarchy. The posted p values should therefore not be assumed to have been adjusted unless the registry explicitly identifies such an adjustment.

The primary efficacy population is defined as randomized participants who received at least 1 dose of investigational product, excluding participants from a site found to have serious GCP noncompliance issues. That definition is important because it determines which participants contributed to the primary efficacy analysis. The registry reports primary outcome group counts of 169, 171, and 164. It does not provide the full participant flow or a detailed explanation of how each other outcome’s analysis population was formed.

Missing data can affect both the estimate and its uncertainty, particularly when the likelihood of missingness is related to a participant’s health status or treatment assignment. The record does not report the amount or reasons for missing primary endpoint measurements, the imputation method, or sensitivity analyses examining alternative assumptions about missing outcomes. Those details are needed to evaluate how robust the results are to incomplete follow-up. The status is terminated, but the effect of termination on outcome collection and follow-up is not reported in the registry record.

The registry identifies the primary analysis method as a Coefficient Regression Model, but the full specification, covariates, assumptions, and diagnostic checks are not reported in the registry record. Likewise, the original sample-size justification, interim analysis plan, and detailed missing-data strategy are not reported. These are limits on what can be assessed from the record; they do not establish that a particular method was or was not used.

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 (6.9%), pneumonia (2.3%), pulmonary embolism (2.3%), covid-19 pneumonia (1.7%), acute myocardial infarction (1.1%).

The safety results report serious adverse events for 38 participants in the GLPG1690 600 mg group, 38 in the GLPG1690 200 mg group, and 36 in the placebo group. The corresponding numbers at risk are 174, 175, and 174. Deaths are reported for 12 participants in the 600 mg group, 8 in the 200 mg group, and 8 in the placebo group. These are counts during the recorded study period, not estimates of the cause of an event or a comparison adjusted for differences in exposure or follow-up.

The registry lists serious adverse event terms including idiopathic pulmonary fibrosis at 6.9%, pneumonia at 2.3%, pulmonary embolism at 2.3%, COVID-19 pneumonia at 1.7%, acute myocardial infarction at 1.1%, and coronary artery disease at 1.1%. These listed terms do not by themselves show that an event was caused by study treatment. The record excerpt does not provide a detailed causal assessment, event timing, or a complete account of all safety outcomes.

Safety counts should be read in the context of the trial’s status, follow-up, and exposure. The mean exposure descriptions differ by arm, and the registry does not provide enough information to make a time-adjusted safety comparison. The counts alone cannot establish that one group had greater or lesser treatment-related risk.

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

The primary estimates describe the difference in annual FVC decline between each GLPG1690 dose group and placebo, with local standard of care used in all groups. The sponsor-reported point estimate for the 600 mg comparison is positive, while the estimate for the 200 mg comparison is negative. Both confidence intervals include zero and extend in both directions. Thus, the posted results leave uncertainty about the direction and size of either dose’s difference from placebo on this endpoint.

This is not evidence that the groups are equivalent. A conclusion of equivalence would require an appropriate design, a prespecified margin defining what differences count as equivalent, and an analysis showing that the uncertainty lies within that margin. Such a margin and an equivalence analysis are not reported in the registry record. Likewise, the results should not be described as proving that GLPG1690 does or does not alter the course of IPF.

The trial’s primary endpoint is one measure of lung function over the specified follow-up. It does not represent every dimension of disease experience or safety. The registry also includes patient-reported symptoms and health status, progression, hospitalization, and mortality outcomes, each with its own limitations and uncertainty. The posted secondary findings do not remove the uncertainty in the primary comparison, and unadjusted secondary tests should be interpreted cautiously in the setting of multiple outcomes.

The findings apply to the trial’s enrolled population, treatment arms, local standard-care context, and recorded follow-up. They do not establish results for people or treatment settings not represented in the trial. The record reports termination but not its reason, and does not report detailed missing-data procedures or the effect of termination on follow-up. Those absences limit interpretation and should not be filled by assumption. The statistics describe what the registry reports; they do not constitute medical advice or an individual treatment recommendation.

18. Why This Trial Matters Statistically

This trial is statistically informative because it tests two doses against a concurrent placebo group while keeping local standard of care in each arm. Random allocation and a parallel-group structure are intended to support a fair comparison by reducing systematic differences in baseline characteristics on average. Placebo comparison also helps separate changes over time from differences associated with assignment to the investigational treatment. The registry identifies quadruple masking, while the official title describes double-blind conduct; the identities of the masked parties are not reported.

The primary endpoint is continuous, and the registry reports both model-based estimates and their uncertainty. This makes it possible to distinguish the estimated direction from the precision of the comparison. In this case, the point estimates differ in direction across doses and both confidence intervals include zero. That combination illustrates why a single estimate or p value is not enough: the range of compatible values is central to understanding what the data can support.

The trial also illustrates the boundary between sponsor analyses and summary-statistic recalculation. The recalculations are close to the sponsor’s reported results, but they are not the same model. Making that distinction explicit prevents an approximate check from being mistaken for a replacement analysis.

Finally, the registry record shows how much interpretive context matters. It lists many outcomes and analyses, but does not report the multiplicity strategy, original sample-size justification, detailed missing-data methods, or reason for termination. These omissions constrain how fully the statistical plan and robustness of the results can be evaluated. Such limits are part of the evidence record, not a reason to infer unreported procedures.

19. Limitations

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

The registry reports the primary outcome and sponsor analyses, but does not provide the full statistical model specification, covariates, diagnostics, or participant-level data. As a result, the model cannot be independently reproduced from the record. Recalculations from summary statistics are approximate and unadjusted; they cannot account for details that may be included in the sponsor’s model.

The registry does not report the original sample-size justification, the assumptions used to design the trial, or whether interim analyses were planned. The planning illustrations based on observed effects therefore should not be confused with the trial’s actual design rationale. The registry also does not report whether or how multiplicity was controlled across the two dose comparisons and numerous outcome measures.

Detailed missing-data information is not reported, including the amount and reasons for missing primary endpoint measurements, the method for handling missing observations, and sensitivity analyses. Although the primary efficacy population definition is stated, full participant flow and outcome-specific analysis populations are not reported for all measures. These gaps prevent a complete assessment of how exclusions and incomplete follow-up might affect estimates.

The registry status is terminated, but the reason for termination and its effect on follow-up are not reported in the registry record. The arm descriptions include mean exposure information, but the available record does not provide enough context to interpret exposure differences or assess their consequences for efficacy and safety comparisons. Safety counts are not time-adjusted in the information, and event attribution is not detailed. These limitations call for restraint in interpreting the estimates; they do not, by themselves, determine the direction of any bias.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Clinical Study to Test How Effective and Safe GLPG1690 is for Subjects With Idiopathic Pulmonary Fibrosis (IPF) When Used Together With Standard of Care — NCT03711162.
• 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

NCT03711162 is a randomized, parallel-group, placebo-controlled phase 3 trial of GLPG1690 added to local standard of care for idiopathic pulmonary fibrosis. The study compared 600 mg and 200 mg once-daily doses with matching placebo. Its primary endpoint was the annual rate of decline in FVC up to week 52.

The sponsor reported a 600 mg versus placebo difference of 22.7 mL/year and a 200 mg versus placebo difference of -26.7 mL/year. Both 95% confidence intervals include zero. The registry records the study as terminated and does not report the reason. Its primary efficacy set and outcome counts are described, but detailed multiplicity, missing-data, and original sample-size methods are not reported in the registry record.