Autoantibody Reduction Therapy in Patients With Idiopathic Pulmonary Fibrosis: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Autoantibody Reduction Therapy in Patients With Idiopathic Pulmonary Fibrosis (NCT01969409), a randomized phase 2 study. The primary outcome is Autoantibodies to Human Epidermoid (HEp)-2 Cells.

2. Clinical Question

The question is about a measured laboratory outcome, not a direct measure of lung function or clinical events. The registry rationale proposes that autoantibodies might be involved in IPF-related lung damage; this study's primary endpoint assesses titers rather than establishing that proposed mechanism. The clinical interpretation therefore needs to keep the biomarker result distinct from outcomes such as forced vital capacity, survival, adverse events, or hospitalizations.

3. Trial Design

This was a phase 2, randomized, parallel-group study with triple masking. The registry lists University of Alabama at Birmingham as the sponsor and records the condition as ambulatory IPF. The study status is completed. The recorded study start is 2014-01, and the primary completion date is 2019-01-31. Enrollment was 58.

Participants were assigned to rituximab or placebo. Rituximab was given intravenously on two occasions, separated by 14 days. The comparator was intravenous placebo consisting of 5% dextrose in water, administered identically to rituximab. The triple-masking label indicates that masking was used at multiple levels, but which specific roles were masked is not reported in the registry record. The method used to generate the randomized allocation and any details of allocation concealment are also not reported in the registry record.

The primary endpoint was anti-HEp-2 autoantibody titer, assessed from baseline to 9 months, with the month 9 result reported. The primary endpoint population notes that 7 were not analyzed: 4 deaths, 2 transplants, and 1 dropout. The arm summaries for that endpoint list 25 for placebo and 26 for rituximab. These analysis counts should not be confused with the enrollment figure: the registry does not give a full participant-flow account explaining all differences among enrolled, assigned, and analyzed groups.

The registry lists secondary outcomes involving HSP70 autoantibodies, forced vital capacity, adverse events, acute exacerbations, absolute survival percentage, transplant-free survival, and hospitalizations. Detailed numerical results are posted for only some of these outcomes. The trial's original sample-size justification, intended primary analysis model, analysis populations, and any interim-analysis plan are 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.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: 7 not analyzed: 4 deaths, 2 transplants, 1 dropout

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 Autoantibodies to Human Epidermoid (HEp)-2 Cells, measured over baseline to 9 months.

The primary endpoint is autoantibodies to human epidermoid (HEp)-2 cells, expressed as a titer. The registry describes titers measured by indirect immunofluorescence assay over 9 months and reports the month 9 result. A titer represents the highest dilution of a participant's plasma at which the autoantibodies can still be detected. Higher titers indicate greater autoantibody concentrations.

This endpoint was selected to assess whether rituximab was associated with a change in an immune marker relevant to the study's proposed rationale. The registry background states that autoantibodies might contribute to lung injury in IPF and that rituximab was being studied as a way to reduce them. The titer is therefore a biomarker measure, not a direct measure of lung function, symptoms, survival, or the overall course of IPF. A difference in this laboratory measure alone would not establish that a change in autoantibodies leads to a clinical benefit.

The endpoint summaries report means and standard errors for the two groups. At month 9, the placebo mean was 288.0 and the rituximab mean was 177.0. The comparison is expressed as the rituximab mean minus the placebo mean, yielding an unadjusted mean difference of -111.0. Its confidence interval is broad and includes zero, so the posted estimate remains compatible with a range of possible differences, including no mean difference. The registry notes that 7 were not analyzed for this endpoint, with deaths, transplants, and dropout listed as reasons. How those missing endpoint values were handled in the trial's own analysis is not reported in the registry record.

7. Results Posted in the Registry

• Rituximab: mean 177.00 versus 288.00 on control; difference -111.00 (95% CI -246.93 to 24.93), standardized effect d = -0.45; z-test p = 0.109.

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.

Changes in Anti-Heat Shock Protein 70 (HSP70) Autoantibodies

• 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:
  • Rituximab: mean 0.83 versus 1.00 on control; difference -0.17 (95% CI -0.47 to 0.13), standardized effect d = -0.31; z-test p = 0.265.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Rituximab and the control. The interval gives the range of effects that remain compatible with the data.

Changes in Forced Vital Capacity (FVC)

• 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:
  • Rituximab: mean 2.50 versus 2.60 on control; difference -0.10 (95% CI -0.52 to 0.32), standardized effect d = -0.13; z-test p = 0.638.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Rituximab and the control. The interval gives the range of effects that remain compatible with the data.

Absolute Survival Percentage

• 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:
  • Rituximab: mean 93.00 versus 93.00 on control; difference 0.00 (95% CI -13.86 to 13.86), standardized effect d = 0.00; z-test p = 1.000.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Rituximab and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes span several kinds of evidence: another autoantibody measure, a lung-function measure, survival outcomes, and clinical events including adverse events, acute exacerbations, and hospitalizations. This breadth is useful because those outcomes address different questions from the primary biomarker endpoint. A pattern across them can add context, but it should not be treated as though all measures were interchangeable or as though they constitute a single confirmatory result.

Among the secondary outcomes with numerical summaries, the HSP70 autoantibody means were 1.0 for placebo and 0.83 for rituximab; the FVC means were 2.6 liters and 2.5 liters; and the absolute survival percentage means were 93.0 and 93.0. The unadjusted recalculated confidence intervals for their group differences include zero. Those results do not establish a secondary effect, nor do they resolve the primary biomarker comparison. The other listed outcomes include acute exacerbations, transplant-free survival, and hospitalizations, but numerical summaries for them are not reported in the registry record.

Secondary findings generally carry less weight when they are not supported by a prespecified analysis plan and an approach to multiplicity. If many outcomes are examined, some differences can arise by chance. The registry record does not report a multiplicity adjustment or a complete inferential analysis for the secondary outcomes. The listed measures are therefore best read as descriptive context, rather than as a collection of independent confirmations of the primary result.

The primary and secondary measures also differ in meaning and scale. A laboratory titer is not a direct substitute for FVC, survival, or clinical events. Agreement or disagreement across those types of measures would need careful interpretation, including consideration of uncertainty, missing data, and the trial's analysis populations. Since some secondary results are not numerically posted and the planned analysis is not documented, the overall secondary pattern is incomplete.

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

• Changes in Anti-Heat Shock Protein 70 (HSP70) Autoantibodies
• Changes in Forced Vital Capacity (FVC)
• Number of Adverse Events (AE)
• Number of Acute Exacerbations
• Absolute Survival Percentage
• Transplant-Free Survival
• Hospitalizations

9. Statistical Interpretation

10. Statistical Methods Explained

What does a mean difference describe?

A mean difference compares the average outcome in one group with the average outcome in another. For the primary endpoint, the comparison is rituximab minus placebo. A negative value therefore indicates a lower average titer in the rituximab group than in the placebo group. Because higher titers represent greater autoantibody concentrations, the sign has a direct descriptive interpretation for this measure. It does not, by itself, establish why the groups differ or what that difference means for clinical outcomes.

The primary comparison uses the posted group means of 177.0 and 288.0 and reports a mean difference of -111.0. These summaries do not reveal individual participant values, distributions, or the degree of overlap between groups. A mean can be influenced by the distribution of observations, and a group average does not imply that every participant had a value near that average.

What do the standard errors describe?

The registry labels the measure of dispersion as standard error. Standard error concerns the precision of an estimated mean: it describes uncertainty around the group average, rather than the spread among individual participants. A standard deviation, by contrast, is used to describe variation among observations. The posted group standard errors are 63.0 for placebo and 29.0 for rituximab. They should not be interpreted as ranges containing most individual titers.

The registry-derived comparisons use the posted summary statistics to form unadjusted estimates and confidence intervals. They are not a substitute for a trial analysis based on participant-level records, covariate adjustment, or a prespecified model. Such model details are not reported in the registry record. The reported comparison is useful for describing the data as posted, but it cannot account for analysis choices that are not documented.

How should the p-value be understood?

The primary unadjusted p-value is 0.109. In general, a p-value describes how unusual data at least as discrepant as the observed result would be under a specified null model. It is not the probability that the null hypothesis is true, and it does not quantify the clinical importance of a difference. It also depends on the assumptions and analysis used to calculate it. The registry record does not report a full statistical analysis plan or whether the trial used a different inferential model for its own analysis.

Because this p-value is unadjusted, it does not account for examining multiple endpoints or comparisons. When many outcomes are considered, chance alone can make some unadjusted results appear more notable. A multiplicity plan can define how to interpret a collection of tests, but such a plan is not reported in the registry record. The p-value should therefore be read alongside the estimate, its confidence interval, and the context of the other outcomes, not in isolation.

Why does over-dispersion matter?

Over-dispersion is a general issue that arises when observed variation is greater than a statistical model assumes. If a model treats data as less variable than they really are, standard errors can be too small and confidence intervals too narrow, making results appear more precise than warranted. The primary endpoint is reported as a continuous titer with a mean and standard error, but the registry record does not provide participant-level distributions or a model assessment that would establish whether over-dispersion was relevant or how it was handled. The posted summary statistics alone cannot answer that question.

More broadly, continuous outcomes can have distributions that are asymmetric or contain unusually high or low values. The mean and standard error do not provide enough information to assess the shape of the titer distribution. The registry does not report a transformation, robust method, or distributional diagnostic. No claim about those procedures should be inferred from the summary values.

What is recalculated, and what is not known?

The comparisons described as recalculated are simple, unadjusted calculations from the posted group summaries. The record marks no discrepancy between those calculations and another result. This does not mean the registry documents every aspect of the trial's original analysis. The original statistical analysis plan, covariates, handling of missing observations, and inferential methods are not reported in the registry record. Consequently, the recalculated estimates are best treated as transparent descriptive comparisons, not as a reconstruction of an undocumented sponsor analysis.

The same distinction matters for secondary endpoints. Their posted group means and unadjusted comparisons can help describe patterns, but the registry does not list reported analyses for those outcomes. A recalculated comparison cannot establish that the trial's investigators used the same method, nor can it supply a missing multiplicity plan. Statistical interpretation should therefore separate the observed summaries from the trial's unreported analysis decisions.

11. Confidence Intervals and Precision

The primary mean difference is -111.0, and its 95% confidence interval runs from -246.9 to 24.93. In general, a confidence interval gives a range of values compatible with the data under the calculation's assumptions. It conveys uncertainty about the estimated difference, rather than showing the range of individual participants' titers. The interval includes zero, so the posted data do not narrowly distinguish a negative mean difference from no difference or a positive mean difference.

The interval is wide relative to the point estimate: its lower end allows a considerably larger negative difference, while its upper end extends into positive values. Thus, the central estimate should not be treated as a precise measure of the true group difference. The standard errors accompanying the means also indicate that the estimated group averages have uncertainty. They are not standard deviations and do not describe the range of individual measurements.

These intervals are unadjusted recalculations from the posted summaries. They do not incorporate adjustments for multiple outcomes or any undocumented model features. The registry record does not provide an interval from a reported sponsor analysis or a prespecified confidence-interval method. Precision should therefore be understood in relation to this summary-based comparison, not as a guarantee that the interval captures every source of uncertainty in the trial.

The other posted continuous-outcome comparisons also have intervals that include zero: the HSP70 autoantibody mean difference is -0.17 with a 95% confidence interval from -0.469 to 0.129; the FVC mean difference is -0.1 with a 95% confidence interval from -0.517 to 0.317; and the absolute survival percentage mean difference is 0.0 with a 95% confidence interval from -13.86 to 13.86. These intervals are also unadjusted recalculations. They are not evidence that all possible differences are excluded; rather, each retains uncertainty around the group comparison.

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 participants per arm, not totals across both arms. They illustrate sample sizes under stated assumptions using the observed effect as a reference. The calculations assume a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is the stated fraction of the observed effect. The trial's own original design assumptions and sample-size justification are not reported in the registry record.

The 80% power column describes a planning target: under the calculation assumptions, the proposed sample size is intended to give an 80% chance of detecting an effect of the specified size if that effect is present. The 90% power column uses a higher target chance of detection under the same assumptions. These are design calculations, not guarantees about what a future study will find. They are not observed power.

For the primary endpoint, planning for 100% of the observed effect gives 77 participants per arm for 80% power and 102 participants per arm for 90% power. Planning for 75% of the observed effect gives 136 participants per arm for 80% power and 182 participants per arm for 90% power. Planning for 50% of the observed effect gives 305 participants per arm for 80% power and 408 participants per arm for 90% power. The smaller the effect a study aims to detect, the more participants the calculation requires, because a smaller difference is harder to distinguish from sampling variation.

These figures are planning illustrations based on the observed estimate, not evidence about the power of the completed trial. Their interpretation depends on the assumptions and on treating the observed effect as a planning reference. They do not address unreported features such as missing data or multiplicity adjustments.

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 = -111.000; pooled standard deviation σ = 244.451.
2. n = 2 × (1.96 + 0.842)² × 244.451² / -111.000² = 76.1, rounded up to 77 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 <- -111                      # observed difference in means
sigma <- 244.450654425345                     # 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(1969409)
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 = 77 (80% power), 102 (90% power)
 75% of observed effect: n per arm = 136 (80% power), 182 (90% power)
 50% of observed effect: n per arm = 305 (80% power), 408 (90% power)
power.t.test: 77.1 
Simulated power at n = 77 per arm: 0.797 (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 registry record does not report how the trial addressed multiplicity, meaning the increased chance of false-positive findings when several outcomes or comparisons are examined. A prespecified hierarchy, adjustment procedure, or designation of some outcomes as exploratory can affect how much weight to place on secondary tests. None of those details is reported in the registry record. The secondary comparisons described in the posted summaries are unadjusted recalculations, so they should not be interpreted as if multiplicity had been accounted for.

Missing endpoint information is directly noted for the primary outcome: 7 were not analyzed, with 4 deaths, 2 transplants, and 1 dropout listed. The registry record does not explain whether the endpoint summaries use only observed month 9 values, whether any imputation was used, or how missing observations were handled in the trial's own analysis. The analysis population and the rule for including participants in each endpoint are not reported in full. These omissions limit assessment of whether the available summaries could be affected by missingness.

The record does not report an intention-to-treat analysis, a per-protocol analysis, or another named analysis population. It also does not give participant flow by assigned group for the primary endpoint beyond the arm summary counts. The trial's original statistical analysis plan, interim-analysis plan, and sample-size justification are not reported in the registry record. These should not be inferred from the fact that the study was randomized or completed.

Missingness can matter because the observed participants may not represent everyone assigned to a group, particularly when reasons for non-analysis include events that also relate to clinical status. That is a general concern, not a claim that bias occurred in this trial. The registry information does not permit an assessment of the direction or size of any such effect. As a result, the endpoint summaries are informative about the posted observations, but the impact of unreported analysis choices and missing-data handling remains uncertain.

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: right ventricular failure (7.1%), infection (6.7%), worsening respiratory function (6.7%), acute exacerbation of idiopathic pulmonary fibrosis (6.7%), myocardial infarct (6.7%).

The registry reports serious adverse events among 5 participants at risk in the placebo group of 28 and 9 participants at risk in the rituximab group of 30. For other adverse events, it reports 21 affected among 28 at risk for placebo and 24 affected among 30 at risk for rituximab. Deaths are listed as 2 in each group. These are descriptive counts in the registry record; they do not, by themselves, establish that treatment caused or prevented an event.

The registry also lists serious adverse-event terms with percentages: Right ventricular failure, 7.1%; Infection, 6.7%; Worsening respiratory function, 6.7%; Acute exacerbation of idiopathic pulmonary fibrosis, 6.7%; Myocardial Infarct, 6.7%; and cerebral vascular accident, 3.6%. The record does not assign these term percentages to a treatment group in the listed summary, so a group-specific comparison should not be inferred from them.

Counts and percentages need context, including exposure, event definitions, timing, and whether a participant could contribute more than one event. Those details and a formal comparative safety analysis are not reported in the registry record. The figures should therefore be read as reported safety information, not as proof of a causal difference or equivalence between groups.

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

The primary endpoint offers a comparison of month 9 anti-HEp-2 titers. The rituximab group mean was lower than the placebo group mean, and the unadjusted mean difference was -111.0. The 95% confidence interval, from -246.9 to 24.93, includes zero and extends in both directions around no difference. This means the posted summary leaves substantial uncertainty about the size and direction of the underlying group difference.

The result does not establish that rituximab reduced lung injury, improved lung function, changed survival, or altered the clinical course of IPF. The primary endpoint is a laboratory measure, and the study rationale about autoantibodies is a proposed biological explanation rather than a conclusion proven by this endpoint. The primary estimate alone cannot establish a link between a titer change and a clinical outcome.

Likewise, the interval and p-value do not prove that there is no effect. The p-value is 0.109, and the confidence interval includes both negative and positive values. These statistics indicate uncertainty in the posted unadjusted comparison; they do not settle the question in either direction. A non-definitive result should not be converted into a claim of equivalence or into a claim of benefit.

The secondary outcomes cover measures that could provide additional context, but the registry record does not report a complete analysis across them or a multiplicity plan. Some listed outcomes do not have numerical results posted. The safety counts are also descriptive and do not establish causation. In addition, 7 were not analyzed for the primary endpoint, and the handling of those missing values is not reported.

The most defensible conclusion is bounded: the registry's posted means show a lower month 9 anti-HEp-2 titer in the rituximab group, but the unadjusted estimate is imprecise and compatible with no mean difference. The information does not support a definitive conclusion about clinical benefit, harm, or the proposed mechanism. Interpretation should remain tied to the endpoint and analysis that are actually reported.

17. Why This Trial Matters Statistically

This trial is statistically informative because it separates a biological hypothesis from a clinical outcome. The study rationale concerns autoantibodies and possible lung injury in IPF, while its primary endpoint is a titer measured by indirect immunofluorescence. Keeping that distinction clear prevents a biomarker comparison from being mistaken for direct evidence about lung function or survival.

The result also illustrates why an estimate and its precision matter together. The primary mean difference is -111.0, but its confidence interval from -246.9 to 24.93 includes zero and spans a range of plausible group differences. Looking only at the direction of the means would overstate what the data can resolve; looking only at the p-value would discard information about the size and uncertainty of the estimate.

The trial record further demonstrates how missing analysis details affect interpretation. The primary endpoint notes participants who were not analyzed, but the record does not describe the missing-data method, complete analysis populations, or the original statistical plan. Without that information, summary-based recalculations cannot reproduce every possible feature of the investigators' analysis.

Finally, the range of secondary outcomes makes multiplicity and outcome hierarchy relevant. Biomarkers, lung function, survival, and clinical events address different questions, and unadjusted secondary findings need cautious interpretation when no adjustment strategy is reported. The planning illustrations add another useful statistical perspective, but they are not observed power and do not reveal the trial's original design assumptions. Together, these features make the study a case for reading trial results through the estimate, uncertainty, endpoint definition, and completeness of the analysis record—not through a single number alone.

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.

The primary endpoint is a biomarker rather than a direct clinical outcome. Although the registry describes why autoantibodies were of interest, the titer does not itself measure lung injury, symptoms, or disease progression. The record therefore cannot establish that a change in this measure corresponds to a clinically meaningful change.

The primary summary excludes 7 participants from analysis, with deaths, transplants, and dropout listed as reasons. The record does not describe how their missing endpoint values were handled, whether the analysis used imputation, or whether the reported arm summaries follow a prespecified analysis population. This limits evaluation of the potential effect of missing data.

Several analysis details are not reported in the registry record: the original statistical plan, model, multiplicity approach, allocation-concealment procedures, and interim-analysis plan. The posted comparisons are unadjusted recalculations from group summaries and cannot account for undocumented methods or participant-level characteristics. Standard errors and means also do not show the individual titer distributions.

The secondary outcome record is incomplete for interpretation: numerical results are not posted for every listed outcome, and reported analyses are not listed for the posted secondary summaries. The serious adverse-event term percentages are not assigned to a group in the listed summary. These constraints make broad claims about consistency across endpoints or comparative safety unsupported by the registry information alone.

Lastly, the planning illustrations use the observed effect as a reference. They should not be treated as the original design justification or as evidence of the completed study's power. The registry's original sample-size assumptions are not reported.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Autoantibody Reduction Therapy in Patients With Idiopathic Pulmonary Fibrosis — NCT01969409.
• Registry record last updated 2024-08-21; status last verified 2024-08.
• Results first posted 2021-11-18.
• 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

NCT01969409 is a completed, randomized, triple-masked, parallel-group phase 2 study sponsored by University of Alabama at Birmingham. It enrolled 58 people with ambulatory IPF and compared intravenous rituximab with intravenous placebo. Rituximab was scheduled on two occasions, 14 days apart.

The primary endpoint was month 9 anti-HEp-2 autoantibody titer. The reported means were 288.0 for placebo and 177.0 for rituximab; the unadjusted mean difference was -111.0, with a 95% confidence interval from -246.9 to 24.93 and an unadjusted p-value of 0.109. The interval includes zero, and the estimate is imprecise.

The record lists secondary measures involving HSP70 autoantibodies, FVC, survival, adverse events, acute exacerbations, transplant-free survival, and hospitalizations. The original statistical plan, multiplicity approach, and missing-data handling are not reported in the registry record. The available results support cautious description of the posted summaries, not a definitive conclusion about clinical benefit or harm.