Safety and Efficacy of a Lysophosphatidic Acid Receptor Antagonist in Idiopathic Pulmonary Fibrosis: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Safety and Efficacy of a Lysophosphatidic Acid Receptor Antagonist in Idiopathic Pulmonary Fibrosis (NCT01766817), a randomized phase 2 study. The primary outcome is Change From Baseline in Forced Vital Capacity (FVC) Rate to Week 26.

2. Clinical Question

3. Trial Design

This was a phase 2, randomized, triple-masked, parallel-group study of BMS-986020 in idiopathic pulmonary fibrosis. The registry record lists Bristol-Myers Squibb as sponsor, enrollment of 325, a start date of 2013-01-31, primary completion on 2016-02-29, and status as completed. Participants were assigned to one of two active dosing schedules or matching placebo.

The active regimens were 600 mg once daily and 600 mg twice daily, each for 26 weeks. The placebo regimen was matching tablets taken twice daily for 26 weeks. The randomized and masked design is intended to support a fair comparison by reducing systematic differences between groups and limiting the influence of treatment knowledge on care or measurement. The registry record does not report details of how the randomization sequence was generated, how allocation was concealed, or which roles were included in triple masking.

The primary outcome concerns change in forced vital capacity from baseline to Week 26. The primary outcome description identifies an intent-to-treat population of all randomized participants, while clarifying that the reported number analyzed means the number evaluable for the outcome. The posted primary outcome has 42 evaluable participants in the once-daily group, 43 in the twice-daily group, and 40 in the placebo group. Those outcome counts are not the same as the registry’s overall enrollment figure; the reasons for the difference are not reported in the registry record.

Secondary measures cover walking distance, shortness of breath, lung imaging, lung function, quality of life, and clinical events. The registry lists 17 outcome measures, with 16 secondary outcomes posted. The registry record does not report the original sample-size justification, the planned statistical analysis in sufficient detail to evaluate it, or whether interim analyses were conducted.

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: Total 325 participants were enrolled,out of which 143 participants were randomized and treated. Reasons for not being treated were:Screening HRCT or Pulmonary function tests did not meet study criteria and "Other" reasons

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Intent-to-treat (ITT) population included all randomized participants. Here 'N' 'number of participants analyzed' signifies number of participants who were evaluable for this outcome measure.

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 Change From Baseline in Forced Vital Capacity (FVC) Rate to Week 26, measured over Baseline, Week 26.

Forced vital capacity (FVC) is the total volume of air a participant can exhale during a forced spirometry test. The registry describes it as an important measure of lung function and specifies that the test uses a tube connected to a machine to measure air moved out of the lungs after an inhaled bronchodilator. The endpoint is expressed in liters and compares the measurement at baseline with the measurement at Week 26.

The study’s stated purpose was to determine whether BMS-986020 could reduce decline in FVC over 26 weeks compared with placebo. FVC is useful for this question because it provides a quantitative measure that can be compared across participants and treatment groups. A change score focuses on how the measure changes during the study rather than only on the value at a single visit.

The primary outcome title refers to an FVC “rate,” but the posted outcome is described as mean change from baseline, in liters, at Week 26. The registry record does not report a rate unit or a separate rate-estimation method. The reported group means are therefore best read as mean changes over the stated follow-up, not as a newly calculated rate per unit of time.

7. Results Posted in the Registry

• BMS-986020 600 mg Once Daily: mean -0.08 versus -0.14 on control; difference 0.06 (95% CI -0.03 to 0.15), standardized effect d = 0.29; z-test p = 0.180.
• BMS-986020 600 mg Twice Daily: mean -0.05 versus -0.14 on control; difference 0.09 (95% CI -0.01 to 0.18), standardized effect d = 0.40; z-test p = 0.067.

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 Six-minute Walk Test (6MWT) Distance to Week 26

• 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:
  • BMS-986020 600 mg Once Daily: mean -14.20 versus 10.30 on control; difference -24.50 (95% CI -46.80 to -2.20), standardized effect d = -0.48; z-test p = 0.031.
  • BMS-986020 600 mg Twice Daily: mean 6.10 versus 10.30 on control; difference -4.20 (95% CI -27.59 to 19.19), standardized effect d = -0.08; z-test p = 0.725.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for BMS-986020 600 mg Once Daily 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 BMS-986020 600 mg Twice Daily and the control. The interval gives the range of effects that remain compatible with the data.

Mean Change From Baseline in the University of California at San Diego Shortness of Breath Questionnaire (UCSD SOBQ) Total Score as a Measure of Dyspnea to Week 26

• 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:
  • BMS-986020 600 mg Once Daily: mean 3.80 versus 3.90 on control; difference -0.10 (95% CI -7.96 to 7.76), standardized effect d = -0.01; z-test p = 0.980.
  • BMS-986020 600 mg Twice Daily: mean -1.70 versus 3.90 on control; difference -5.60 (95% CI -14.11 to 2.91), standardized effect d = -0.28; z-test p = 0.197.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between BMS-986020 600 mg Once Daily 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 BMS-986020 600 mg Twice Daily and the control. The interval gives the range of effects that remain compatible with the data.

Mean Change From Baseline in Forced Vital Capacity (FVC) to Week 26

• 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:
  • BMS-986020 600 mg Once Daily: mean -0.08 versus -0.14 on control; difference 0.06 (95% CI -0.03 to 0.15), standardized effect d = 0.29; z-test p = 0.180.
  • BMS-986020 600 mg Twice Daily: mean -0.05 versus -0.14 on control; difference 0.09 (95% CI -0.01 to 0.18), standardized effect d = 0.40; z-test p = 0.067.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between BMS-986020 600 mg Once Daily 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 BMS-986020 600 mg Twice Daily and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover several dimensions: six-minute walk distance, shortness of breath, FVC, quantitative lung fibrosis, carbon monoxide diffusing capacity, quality of life, and clinical events. This breadth can help describe whether the primary lung-function outcome sits within a broader pattern across measured domains. It also creates many opportunities for apparent differences to arise by chance when results are examined separately.

The posted secondary summaries do not form a uniformly consistent pattern across measures and dosing schedules. Some group means differ in direction, while other comparisons show little separation. For the primary FVC outcome, both active-group mean changes were less negative than placebo, but the unadjusted intervals included zero. The secondary results should be considered alongside that uncertainty rather than as independent confirmation of a single conclusion.

Unadjusted secondary comparisons carry less weight because the registry lists many secondary measures and the record does not report a multiplicity adjustment, a testing hierarchy, or sponsor-reported analyses. When many hypotheses are evaluated, the chance of seeing at least one seemingly notable result can rise. A p-value from an individual secondary comparison does not account for the full set of outcomes, and a result that looks notable in isolation may not remain so under a prespecified adjustment.

There are no reported analyses for the listed secondary measures in the registry record. The available numerical comparisons are therefore descriptive, unadjusted recalculations from the posted arm summaries. They are useful for understanding the direction and rough scale of observed group differences, but should not be treated as definitive evidence across multiple domains. The registry record also does not report clinical-importance thresholds for these measures, so statistical separation cannot be equated with a meaningful change for participants.

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

• Geometric Mean Ratio (GMR) of Quantitative Lung Fibrosis (QLF) Score at Week 26 to Baseline
• Mean Change From Baseline in Six-minute Walk Test (6MWT) Distance to Week 26
• Mean Change From Baseline in the University of California at San Diego Shortness of Breath Questionnaire (UCSD SOBQ) Total Score as a Measure of Dyspnea to Week 26
• Mean Change From Baseline in Forced Vital Capacity (FVC) to Week 26
• Mean Change From Baseline in Quality of Life as Measured by the Medical Outcomes Study (MOS) 36-Item Short-Form Health Survey (SF-36) to Week 26
• Number of Participants With Death or Non-Elective Hospitalization
• Number of Participants With Death or Respiratory Hospitalization or 10 Percent (%) Decline in Absolute Volume of FVC or 25-Meter Loss in 6-Minute Walk Distance (6MWD)
• Mean Change From Baseline in Carbon Monoxide Diffusing Capacity (DLCO) to Week 26

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous: each participant has an FVC change measured in liters, and the posted group result is a mean with a standard deviation. A mean describes the group’s average change. A standard deviation describes how spread out participant results are around that average. These answer different questions: the mean indicates the central tendency, while the standard deviation characterizes variation among participants.

What does a mean difference represent?

The comparison is the active group’s mean change minus the placebo group’s mean change. A positive difference in this setting means the active-group change is numerically higher, or less negative, than the placebo-group change. For the primary outcome, the once-daily comparison is 0.06 liters and the twice-daily comparison is 0.086 liters. These differences are unadjusted recalculations from the posted arm summaries. They do not establish that a treatment caused the difference, and they do not account for other outcomes or comparisons.

Why does variability matter?

The standard deviations are 0.224 liters for once-daily dosing, 0.244 liters for twice-daily dosing, and 0.180 liters for placebo. Greater participant-to-participant variation makes a group mean less precise when group size is held constant. A pooled standard deviation combines within-group variability for a two-group comparison; the posted pooled values are 0.204 and 0.216 for the two primary comparisons. The standardized difference values, 0.294 and 0.399, express the differences in relation to pooled variability. These are descriptive scales, not probabilities of benefit.

What does a confidence interval communicate?

A confidence interval gives a range of values compatible with the estimated comparison under the calculation’s assumptions. The primary intervals are -0.028 to 0.148 liters for once-daily dosing and -0.006 to 0.178 liters for twice-daily dosing. Each includes zero, the value representing no mean difference. The intervals also include positive values, indicating that the data are compatible with a positive difference of varying size. An interval is not a guarantee that the true value lies within its endpoints, and it does not give the probability that a particular treatment effect is true.

How should the p-values be read?

The unadjusted p-values are 0.18 for once-daily dosing and 0.067 for twice-daily dosing. A p-value measures how unusual data at least as incompatible with a null model would be if that model and the calculation assumptions were correct. It is not the probability that the null hypothesis is true, nor a measure of clinical importance. Because these values are unadjusted, they do not account for the broader set of outcomes and comparisons in the study. The registry record does not report a multiplicity procedure or a formal analysis plan against which to interpret them.

Why does over-dispersion matter?

General statistical explanation: over-dispersion means observed variability is greater than a model assumes. When a model understates variability, standard errors can be too small and intervals can be too narrow, making results appear more precise than they are. For a continuous endpoint, the spread of participant measurements is directly relevant to uncertainty in a group mean. The posted standard deviations show variation in FVC changes, but the registry record does not report a model diagnostic or an over-dispersion assessment.

The sample-size planning illustrations use a normal approximation and assume equal allocation between the two groups in a comparison. They are based on the observed effect or stated fractions of it, not the trial’s original design plan. Such calculations help show how sample size responds to assumed effect size and variability, but they do not replace an analysis of the trial’s actual design or observed data.

Finally, the distinction between the intent-to-treat population and participants evaluable for an endpoint matters. The primary outcome description defines intent-to-treat as all randomized participants, but says the reported analysis count is the number evaluable. Without information about missing outcome values and the analysis method, readers cannot determine whether the posted group summaries include every randomized participant or how incomplete follow-up may have affected the estimates.

11. Confidence Intervals and Precision

The primary comparisons are accompanied by intervals that span zero. For once-daily BMS-986020, the estimated mean difference versus placebo is 0.06 liters, with interval endpoints -0.028 and 0.148. For twice-daily dosing, the estimated difference is 0.086 liters, with endpoints -0.006 and 0.178. The registry record does not state the confidence level for these recalculated intervals, so no confidence percentage should be attached to them.

Both intervals allow for a small difference in the negative direction as well as a positive difference. Their widths indicate that the estimates do not pin down a narrow range of plausible mean differences. That uncertainty is important: the point estimate alone gives a single number, but the interval shows how much the estimate may vary given the observed group sizes and spread under the calculation assumptions.

The group standard deviations are substantial relative to the mean differences, and each primary comparison involves 40 placebo participants and either 42 or 43 active-group participants. With this amount of outcome variability and these group sizes, uncertainty remains even when the estimated differences are positive. A p-value cannot resolve that uncertainty; it reduces the data to a single measure under a null model, whereas the interval displays a range of effect sizes compatible with the calculation.

These intervals are unadjusted recalculations, not reported sponsor analyses. They do not reflect adjustment for multiple comparisons, and the registry record does not provide a planned inferential model or missing-data method. They should therefore be read as a measure of precision for the simple comparisons, not as a complete account of uncertainty under every possible analysis.

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 give participants per arm for 80% power and participants per arm for 90% power. They are not total event counts: the endpoint comparisons are continuous, so the figures describe the number of participants in each of two equally allocated groups. For example, the planning rows are framed as detecting 100%, 75%, or 50% of the observed effect. These are hypothetical planning choices, not additional findings from the trial.

The calculations assume a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. They use the stated fraction of the observed effect as the effect to detect. The trial’s own original sample-size assumptions and justification are not reported in the registry record. The figures are planning illustrations based on observed summaries, not observed power.

In plain terms, 80% power means that a study designed under the stated assumptions would have an 80% chance of detecting an effect of the specified size using the calculation’s decision rule, if that effect and assumptions were correct. The 90% column represents a higher chance under those same assumptions. Greater power generally requires more participants when other assumptions stay fixed.

The illustrations also show why smaller effects need more participants: a smaller difference is harder to distinguish from ordinary variation. The table entries are sensitive to the estimated effect, which can itself be unstable in a small study. These planning values should not be read as evidence that the trial was designed with those group sizes or that it achieved the stated power.

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 = 0.060; pooled standard deviation σ = 0.204.
2. n = 2 × (1.96 + 0.842)² × 0.204² / 0.060² = 181.1, rounded up to 182 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 <- 0.06                      # observed difference in means
sigma <- 0.203800339793632                     # 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(1766817)
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 = 182 (80% power), 243 (90% power)
 75% of observed effect: n per arm = 322 (80% power), 432 (90% power)
 50% of observed effect: n per arm = 725 (80% power), 970 (90% power)
power.t.test: 182.1 
Simulated power at n = 182 per arm: 0.793 (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. Multiplicity, Missing Data and Analysis Populations

The study has one primary outcome and numerous secondary outcomes, including several measures of lung function, symptoms, function, quality of life, and clinical events. The registry record does not report how the investigators controlled the overall risk of false-positive findings across these outcomes, whether comparisons were arranged in a hierarchy, or whether any secondary results were intended to be confirmatory. The recalculated p-values are unadjusted and should be interpreted as individual comparisons rather than as a family of controlled tests.

The primary outcome description says that the intent-to-treat population included all randomized participants, but also defines the reported number analyzed as participants evaluable for that outcome. The posted primary analysis counts are 42, 43, and 40 across the three groups. The registry record does not report why other enrolled participants are not represented in those outcome counts, the extent or pattern of missing FVC measurements, or the method used to handle missing data.

Missingness can affect interpretation if participants with unavailable measurements differ from those with observed measurements. General statistical explanation: complete-case summaries describe participants with observed data and may not represent all randomized participants when missingness is related to outcomes or participant characteristics. Methods such as imputation or model-based approaches can make different assumptions about missing values, but the registry record does not report whether any such method was used.

The record also does not report the specific model used for the primary analysis, covariate adjustments, sensitivity analyses, or interim analyses. The reported comparison estimates are simple unadjusted recalculations from summary statistics, not a substitute for the sponsor’s complete analysis. Without details of prespecification and analysis methods, readers cannot assess whether the posted results follow the intended statistical plan or how robust they are to alternative assumptions.

15. 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: overdose (12.8%), idiopathic pulmonary fibrosis (6.2%), pneumonia (6.2%), acute myocardial infarction (4.3%), acute respiratory failure (2.1%).

The registry reports participants with serious adverse events in each group: 9 of 48 at risk in the once-daily group, 16 of 48 in the twice-daily group, and 12 of 47 in the placebo group. It also reports participants with other adverse events: 21 of 48, 40 of 48, and 25 of 47, respectively. Deaths are reported as 2, 2, and 1 across the same groups.

These are group-level counts of participants affected, not a measure of whether an event was caused by study treatment. The registry record does not provide enough detail to attribute individual events or deaths to a particular treatment. It lists serious-event terms and percentages, including overdose, idiopathic pulmonary fibrosis, pneumonia, acute myocardial infarction, acute respiratory failure, and hypoxia. The precise denominator used for those term percentages is not reported in the registry record.

Differences in counts should be interpreted cautiously because the numbers at risk are not identical and event descriptions do not establish causation. These safety summaries describe what was recorded in the trial; they do not by themselves determine comparative risk or establish a complete safety profile.

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

The posted primary results describe average FVC changes through Week 26 in three study groups. Mean change was -0.136 liters with placebo, -0.076 liters with once-daily BMS-986020, and -0.05 liters with twice-daily BMS-986020. The unadjusted mean differences versus placebo were positive, but their intervals included zero. This means the observed summaries show numerical separation while leaving meaningful uncertainty about the size and direction of the underlying group differences.

These results do not establish that either dosing schedule reduced FVC decline. Nor do they establish that there was no difference. The estimates and intervals are compatible with a range of possibilities, and the registry record does not include a reported sponsor analysis or a prespecified clinical-importance threshold. Statistical uncertainty should not be confused with proof of equivalence or with proof of a treatment effect.

The findings also do not settle whether any difference would matter to participants. That judgment would require a clinically meaningful threshold and consideration of the broader evidence, neither of which is reported in the registry record. Secondary outcomes may add context, but the registry reports many such measures and does not describe multiplicity control or a confirmatory testing sequence.

Safety counts are also descriptive. Counts of participants with adverse events or deaths do not, alone, show that an event was caused by treatment or establish how the groups compare after accounting for exposure and other factors. The posted information supports reading the recorded numbers, not making a treatment recommendation or a definitive benefit-risk conclusion.

Overall, the registry record documents a randomized, triple-masked phase 2 comparison and numerical outcome summaries. The posted primary estimates are not precise enough to resolve whether the dosing schedules differ from placebo on mean FVC change. A complete interpretation would require the planned analysis, handling of missing data, multiplicity approach, and fuller results, which are not reported in the registry record.

17. Why This Trial Matters Statistically

This trial illustrates why a point estimate and its uncertainty should be read together. The primary comparisons are positive, but each interval includes zero. A reader who considers only the direction of the means could overstate what the data establish; a reader who considers only a p-value could miss the range of differences still compatible with the results.

It also shows the importance of separating a trial’s overall enrollment from the number contributing to a particular outcome. The record lists enrollment of 325, while the posted primary outcome counts are 42, 43, and 40. The registry does not explain this difference, so the outcome-specific denominator and missing-data process deserve attention before drawing strong conclusions.

The range of secondary outcomes raises a further statistical issue. A trial can examine multiple related measures, but isolated unadjusted comparisons should not be interpreted as if only one question had been asked. Without a reported multiplicity plan or analysis hierarchy, the secondary results are more appropriately treated as exploratory descriptions.

Finally, the planning illustrations help explain how assumed effect size and variability influence required sample size. They are not a record of the study’s original design decisions and do not describe what power the completed study had. Keeping planning calculations distinct from observed results is essential when using a small phase 2 trial to understand uncertainty.

18. Limitations

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

Several trial-specific limitations affect statistical interpretation. The posted primary outcome counts are much smaller than the overall enrollment figure, and the registry record does not explain the difference. It states that the outcome analysis count is the number evaluable, but does not report reasons for non-evaluability, missing-data patterns, or methods used to address missing measurements.

The registry record does not include reported analyses for the primary or listed secondary comparisons. The available estimates and intervals are unadjusted recalculations from posted group summaries. As a result, they may not correspond to a prespecified sponsor model, and they do not incorporate any adjustment for multiple outcomes or comparisons. The original statistical analysis plan, sample-size justification, and interim-analysis information are not reported in the registry record.

The primary endpoint title uses the word “rate,” while the posted outcome is a mean change in liters from baseline to Week 26. The record does not report a rate unit or a separate rate calculation. This makes it important to describe the posted measure as mean change over the stated period rather than infer a different endpoint.

The study is described as randomized and triple-masked, but the registry record does not provide details of sequence generation, allocation concealment, or masking roles. It also does not specify a clinical-importance threshold for FVC or the secondary outcomes. The safety summaries provide counts and selected serious-event terms, but do not establish event causality or report the denominator for the listed term percentages.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Safety and Efficacy of a Lysophosphatidic Acid Receptor Antagonist in Idiopathic Pulmonary Fibrosis — NCT01766817.
• Registry record last updated 2020-08-11; status last verified 2020-08.
• Results first posted 2019-05-22.
• 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.

22. Record Summary

This completed phase 2 study randomized participants with idiopathic pulmonary fibrosis to BMS-986020 600 mg once daily, BMS-986020 600 mg twice daily, or matching placebo for 26 weeks. The study was parallel-group and triple-masked, with registry enrollment of 325.

The primary outcome was mean change in FVC from baseline to Week 26. Mean changes were -0.076 liters and -0.05 liters in the active groups and -0.136 liters with placebo. Unadjusted recalculated differences versus placebo were 0.06 liters and 0.086 liters; both intervals included zero. The registry record does not report sponsor analyses, the original sample-size justification, multiplicity methods, or missing-data handling. The results therefore describe observed group summaries with substantial uncertainty, not a definitive treatment conclusion.