Study of Efficacy and Safety of LOU064 in Inadequately Controlled Asthma Patients: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study of Efficacy and Safety of LOU064 in Inadequately Controlled Asthma Patients (NCT03944707), a randomized phase 2 study. The primary outcome is Change From Baseline in Pre-dose FEV1 at Week 12.

2. Clinical Question

3. Trial Design

This was a randomized, parallel-group, placebo-controlled phase 2 study of LOU064 in participants with inadequately controlled asthma. The registry describes subject and investigator blinding and records quadruple masking. The planned treatment period in the study description was 12 weeks, with background budesonide/formoterol therapy. Participants were allocated in a 3:2 ratio to LOU064 100 mg once daily or matching placebo once daily.

The registry lists enrollment of 76 and a terminated status. It gives a study start date of 2019-07-18 and a primary completion date of 2020-04-27. The reason for termination is not reported in the registry record, so the status alone does not establish why the study ended or whether termination changed the conduct or analysis.

The primary endpoint was change from baseline in pre-dose FEV1 at Week 12. Additional posted outcomes cover asthma symptoms, peak expiratory flow, use of short-acting beta agonist puffs, and pharmacokinetic measures of LOU064. Eight outcome measures and seven analyses are listed. The record does not report the original sample-size justification, detailed recruitment progress, or whether any planned analyses changed after termination.

The primary outcome analysis set is described as participants with a valid outcome measurement in the PD analysis set. Different outcome records have different participant counts. The registry does not explain all differences in those counts, so they should not be read as a single common analysis population.

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: After the screening, participants went through a Run-in period of 3-5 weeks where they discontinued their current asthma therapy and were placed on budesonide 80 μg/formoterol 4.5 μg delivered by dry powder inhaler. Afterwards, patients were randomized in 3:2 ratio to receive LOU064 or placebo and continued to use the budesonide/formoterol inhaler.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: PD analysis set including participants with a valid measurement for the 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 Pre-dose FEV1 at Week 12, measured over Baseline, Week 12.

The primary endpoint is change from baseline in pre-dose FEV1 at Week 12, measured in liters. FEV1 is the amount of air that can be forcibly exhaled from the lungs during the first second of a forced exhalation. The registry defines pre-dose FEV1 as the average of two measurements taken 45 minutes and 15 minutes before dosing. Baseline is defined using the corresponding measurements before dosing on Day 1.

Change from baseline provides a way to compare follow-up lung-function measurements with each participant’s baseline measurement, rather than comparing only end-of-study values. The registry states that a positive change is considered favorable. FEV1 is used as a measurable continuous endpoint, allowing the analysis to estimate average changes and a treatment-group contrast. The posted primary result is a model-based estimate, adjusted for baseline pre-dose FEV1 and treatment-by-visit effects.

The result is not a direct description of every participant’s experience. Group means and their uncertainty summarize the analyzed measurements, and the estimates depend on the analysis model and the participants contributing valid data. The registry record does not report an established threshold for interpreting the size of a change in this study, so the numerical contrast alone does not establish how important it would be in practice.

7. Results Posted in the Registry

• LOU064: mean 0.10 versus 0.07 on control; difference 0.03 (95% CI 0.00 to 0.06), standardized effect d = 0.61; z-test p = 0.034.

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.

Change From Baseline in Asthma Symptom Questionnaire-5 Score (ACQ-5) at Week 12

• 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:
  • LOU064: mean -0.95 versus -0.86 on control; difference -0.09 (95% CI -0.18 to -0.00), standardized effect d = -0.62; z-test p = 0.038.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for LOU064 than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change From Baseline in Number of Puffs of SABA Taken Per Day During the Treatment Period

• 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:
  • LOU064: mean -0.19 versus -0.06 on control; difference -0.13 (95% CI -0.19 to -0.08), standardized effect d = -1.25; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for LOU064 than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes span symptom scores, lung-function measures, rescue-medication use, and pharmacokinetic measures. The posted results do not present a consistent pattern of clear separation between LOU064 and placebo across the secondary measures for which comparative analyses are shown. In particular, the registry-reported Bayesian analyses for ACQ-5 and SABA use have intervals that include zero. The broader set of secondary endpoints should be viewed as supporting context rather than as a replacement for the primary endpoint.

These results do not resolve the uncertainty in the primary FEV1 analysis. Secondary outcomes can provide complementary information, but they may differ in measurement properties, analysis populations, and precision. Their results are not interchangeable with the primary endpoint, and one favorable-looking secondary calculation would not by itself establish a consistent treatment pattern.

Unadjusted secondary results carry less weight because several outcomes were assessed. When multiple hypotheses are examined, the chance of at least one apparently notable result can increase even if there is no underlying effect. In general, multiplicity procedures address that issue by adjusting interpretation or testing thresholds. Whether a formal multiplicity strategy was planned or used is not reported in the registry record. Therefore, isolated unadjusted p values should be treated cautiously and should not be interpreted as confirmatory evidence.

The registry lists eight outcome measures, seven analyses, and seven posted secondary outcomes. These counts do not establish how the outcomes were prioritized or whether all planned analyses are represented. A complete interpretation would require a reported analysis plan and fuller information about which outcomes were prespecified, how missing observations were handled, and whether multiplicity was controlled.

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

• Maximum Observed Blood Concentrations (Cmax) of LOU064 at Steady State
• Time to Reach Maximum Blood Concentrations (Tmax) of LOU064 at Steady State
• Area Under the Concentration-time Curve From Time Zero to 24 Hours (AUC0-24h) of LOU064 at Steady State
• Change From Baseline in Asthma Symptom Questionnaire-5 Score (ACQ-5) at Week 12
• Change From Baseline in Mean Morning and Mean Evening Peak Expiratory Flow (PEF)
• Change From Baseline in Number of Puffs of SABA Taken Per Day During the Treatment Period
• Change From Baseline in Daytime and Nighttime Asthma Symptom Score

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous, so it is summarized by a mean change and a treatment-group contrast. The registry’s analysis method is a Bayesian model for repeated measures. In general, a repeated-measures model uses measurements across visits while accounting for their relationship within a participant. The record says the primary analysis adjusted for treatment-by-visit interaction and baseline pre-dose FEV1. It also says a weakly informative prior was considered for the placebo response. Further details of the model specification are not reported in the registry record.

What does the treatment contrast represent?

The contrast is the estimated difference between the LOU064 and placebo groups in change from baseline. The registry reports a net mean difference of 0.030 liters. “Net” identifies the model-based group contrast, rather than either group’s change considered alone. A positive contrast is in the direction of a larger change for LOU064, consistent with the registry’s statement that a positive change is favorable. The estimate does not by itself indicate its precision or clinical importance.

Why is the registry analysis different from the recalculation?

The recalculation is a simple unadjusted comparison of posted group summary statistics. It does not reproduce the Bayesian repeated-measures model or its adjustment for baseline and treatment-by-visit effects. The registry’s primary estimate is close in point value to the recalculated estimate, but its interval and reported p value are substantially different. These methods answer related but not identical statistical questions and use different assumptions. Because the discrepancy flag is true, the sponsor’s own analysis takes precedence; the simple recalculation is a check on the posted summaries, not a replacement for the registered analysis.

In general, model adjustment can change both an estimate and its uncertainty, particularly when data are observed at multiple visits or when the analysis includes baseline information. The registry record does not provide enough detail to independently reproduce the model, examine its diagnostics, or determine exactly why the two uncertainty summaries differ.

What do the interval and p value communicate?

In general, an interval expresses uncertainty around an estimate. A confidence interval has a repeated-sampling interpretation under its statistical procedure, while a Bayesian interval summarizes uncertainty about a parameter conditional on the model and prior. The registry identifies its primary interval as 80% and reports a Bayesian model, so it should be described as the registry’s reported interval rather than silently relabeled as a conventional confidence interval.

A p value summarizes how compatible data are with a specified null model under the method used. It does not state the probability that a treatment effect is true, and it does not measure the size or importance of an effect. The registry reports p values for its Bayesian analyses, but detailed definitions of those values are not reported in the registry record. The unadjusted recalculation p value belongs to a different analysis and should not be substituted for the registry’s result.

Why can over-dispersion matter?

In general, over-dispersion means that observed variability is greater than a model expects. If a model understates variability, its uncertainty estimates can be too narrow and its evidence can appear stronger than warranted. Conversely, a model that accounts for variability appropriately can yield wider uncertainty. The registry record does not report an over-dispersion assessment for this trial, so it is not possible to say whether this issue affected the analyses.

What does the analysis population mean?

The primary outcome population is described as the PD analysis set with a valid measurement for the outcome. This indicates that the reported analysis concerns participants with qualifying outcome data, not necessarily every randomized participant. The record does not fully describe the handling of missing measurements, the number of participants excluded from each analysis, or whether missingness assumptions were tested. Those details matter because analyses based on available measurements can be affected if missingness is related to outcome or treatment assignment.

Statistical methods can organize evidence and express its uncertainty, but they cannot eliminate limitations in the data or replace unreported design details. Interpretation should therefore distinguish the registry’s model-based result, simple summary-statistic recalculations, and the general assumptions associated with each.

11. Confidence Intervals and Precision

The primary registry estimate is 0.030 liters, with an 80% interval extending from -0.060 to 0.119. The interval includes zero and includes estimates in either direction. This means the posted model-based result is not precise enough to distinguish the estimated contrast clearly from no difference under the model’s interval summary. The interval also permits a range of effect sizes broader than the point estimate alone suggests.

The unadjusted recalculation gives a mean difference of 0.03 liters and an interval from 0.002 to 0.058. That interval does not match the registry’s model-based interval. This is not a contradiction that can be resolved by choosing whichever interval appears more favorable: they come from different analyses. The recalculation does not reproduce the repeated-measures model, and the discrepancy flag means the sponsor’s own analysis takes precedence.

In general, an interval describes the range of estimates compatible with a statistical procedure and its assumptions. It is not a guarantee that the true value lies within its limits, nor does it describe the spread of individual participant outcomes. For a Bayesian analysis, interpretation also depends on the model and prior. The registry reports a weakly informative prior for the placebo response, but additional prior and model details are not reported in the registry record.

The primary analysis includes participants with valid outcome measurements in the stated analysis set. The record does not explain all differences among the participant counts across outcomes or fully describe missing-data handling. Consequently, precision should be understood as precision for the analyzed data under the specified analysis, not as a statement that all randomized participants contributed equally or that uncertainty from missing data has been removed.

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 primary effect, not the study’s original design calculation. They assume a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The calculation varies the effect to be detected, using the stated fraction of the observed effect. The original trial’s sample-size assumptions and justification are not reported in the registry record.

Each figure is the number of participants per arm. The 80% power column describes the planned sample size that, under those assumptions, would give an 80% chance of detecting the specified effect if that effect were the true one. The 90% power column uses a higher probability of detection under the same planning framework. The entries for 100% of the observed effect use the full observed effect as the target; the other rows plan for 75% or 50% of that effect. Smaller target effects require more participants per arm because they are harder to distinguish from background variability.

These are planning illustrations, not a reconstruction of the trial’s design and not observed power. They do not account for unreported design choices or possible departures from the calculation assumptions. The study’s randomization used a 3:2 ratio, whereas these illustrations assume equal allocation, so they should not be read as a description of the actual allocation plan. The results are useful for understanding how assumed effect size and desired power relate to sample size, rather than as evidence about the probability that the trial’s result is correct.

The time-to-event convention about total events does not apply to these continuous outcomes. Here the figures refer to participants per arm.

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 = 0.030; pooled standard deviation σ = 0.050.
2. n = 2 × (1.96 + 0.842)² × 0.050² / 0.030² = 42.8, rounded up to 43 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 <- 0.03                      # observed difference in means
sigma <- 0.0495142141207957                     # 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(3944707)
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 = 43 (80% power), 58 (90% power)
 75% of observed effect: n per arm = 77 (80% power), 102 (90% power)
 50% of observed effect: n per arm = 172 (80% power), 229 (90% power)
power.t.test: 43.7 
Simulated power at n = 43 per arm: 0.791 (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 registry’s primary result comes from the sponsor’s Bayesian model for repeated measures, adjusted for treatment-by-visit interaction and baseline pre-dose FEV1. It reports a net mean difference of 0.030 liters, an 80% interval from -0.060 to 0.119, and a p value of 0.664. This is the analysis that should lead the interpretation of the primary endpoint.

The simple recalculation uses posted arm-level means and standard deviations to estimate an unadjusted difference. It gives a mean difference of 0.03 liters, an interval from 0.002 to 0.058, and an unadjusted p value of 0.034. It is a separate calculation, not an independent replication of the Bayesian model, and it does not account for the model’s repeated measurements or stated adjustments.

The point estimates are similar, but the interval and p-value results differ. The discrepancy flag is true, so the sponsor’s own analysis takes precedence. The recalculation can help readers see how a basic comparison of the posted summaries behaves, but it should not override the model-based result. The registry record does not provide sufficient detail to reproduce the sponsor’s model or explain fully why its uncertainty differs from that of the unadjusted calculation.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when several outcomes, comparisons, or analyses are examined. In general, the more statistical questions tested, the greater the chance that at least one result may look unusual by chance alone. Methods such as adjusted significance thresholds or hierarchical testing can address this, but the registry record does not report whether either approach was planned or applied. The posted secondary results should therefore be interpreted as exploratory context unless the record establishes otherwise.

The registry lists eight outcome measures and seven analyses, with seven secondary outcomes posted. The record does not give a full analysis hierarchy, identify a family of tests, or state how the primary and secondary outcomes were handled together. It also does not report interim analyses or stopping rules. These details should not be inferred from the terminated status.

The primary population is described as the PD analysis set, including participants with a valid measurement for the outcome. The registry does not provide a complete account of missing measurements, reasons for missingness, exclusions, or imputation procedures. It is also not reported whether sensitivity analyses examined alternative missing-data assumptions. This matters because the estimate and its precision may depend on who contributed outcome data and how incomplete records were handled.

Participant counts differ across posted outcomes. For example, the primary endpoint arms list 32 and 20 participants, while other outcome records list different counts. The registry does not explain all such differences, so they should not be attributed to a specific cause. The count differences also mean that results from separate outcomes need not describe exactly the same analyzed group.

The registry’s primary analysis is Bayesian and uses a weakly informative prior for the placebo response, but additional prior specifications, model diagnostics, and robustness checks are not reported in the registry record. Together, the unreported multiplicity and missing-data details limit independent assessment of the analysis choices and the stability of the results.

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 non-serious adverse event terms

For serious adverse events, the registry records zero affected participants among 47 at risk in the LOU064 group and zero among 29 at risk in the placebo group. It also records zero deaths in each group. These are counts in the posted safety data; they do not establish that no serious events could occur or that the groups have equivalent safety profiles.

The registry separately lists other, non-serious adverse events affecting 8 participants among 47 at risk with LOU064 and 10 among 29 at risk with placebo. The record does not provide serious adverse event terms, as no top serious terms are listed. It also does not give enough detail to assess event timing, severity categories beyond the serious-event distinction, attribution, or reasons for any differences in the numbers at risk.

Safety counts should be interpreted in relation to the number of participants monitored and the study’s duration. This was a 12-week treatment study, and the numbers at risk differ between groups. The posted counts are descriptive and should not be treated as a definitive comparative safety assessment.

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

The primary endpoint estimates a small positive difference in mean change from baseline between LOU064 and placebo, but the sponsor’s model-based interval is broad and spans zero. The registry-reported result therefore leaves substantial uncertainty about the size and direction of the contrast under that model. The simple unadjusted recalculation gives a different uncertainty summary, but it is not a substitute for the sponsor’s analysis because it does not use the same model or adjustments.

The results describe measurements from this randomized, placebo-controlled study in participants with inadequately controlled asthma. They do not establish what would happen in other populations, over a different treatment duration, or under different study conditions. The registry record also does not report the original sample-size justification, full missing-data strategy, or a multiplicity plan, all of which would help assess how robustly the study addressed its questions.

The status is terminated, but the reason is not reported in the registry record. That status should not be taken as evidence about the results or their cause. Likewise, zero serious adverse events and zero deaths in the posted safety counts do not establish an absence of risk, particularly given the study’s limited duration and group sizes.

Statistical results are not medical advice and do not determine an individual treatment decision. The posted data support a description of the estimates, uncertainty, and analysis limitations; they do not by themselves establish that LOU064 does or does not work. The primary inference should remain anchored to the sponsor’s reported Bayesian analysis, with the recalculation treated as a distinct, unadjusted comparison.

18. Why This Trial Matters Statistically

This trial illustrates why a reported treatment contrast cannot be interpreted apart from its analysis method. The primary endpoint is a continuous measure, but the registry’s main result comes from a Bayesian repeated-measures model, while a simple comparison of group summaries yields a different interval and p value. Similar point estimates do not ensure similar uncertainty conclusions when methods and assumptions differ.

The record also demonstrates the importance of identifying the analysis population. The primary analysis is described as using participants with valid measurements, and participant counts vary across outcomes. Without fuller details on missing data and the reasons for differing counts, readers cannot assume every outcome represents the same group or that missingness has no bearing on estimates.

Multiplicity is another statistical issue. Several secondary outcomes are posted, but the registry does not report a multiplicity strategy. This makes it important to distinguish confirmatory primary evidence from exploratory findings across multiple outcomes. A result should not gain undue weight merely because one unadjusted comparison appears notable.

Finally, planning calculations based on the observed effect are not a record of the original design rationale and are not observed power. The trial’s original sample-size justification is not reported. Keeping design assumptions, observed estimates, model-based inference, and post hoc planning illustrations separate helps prevent overinterpretation of a small study’s results.

19. Limitations

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

The study is listed as terminated, but the reason for termination is not reported in the registry record. Without that information, it is not possible to assess whether termination was related to recruitment, operational circumstances, safety, efficacy, or another cause. No explanation should be inferred from status alone.

The enrollment is listed as 76, but the primary outcome arms list 32 participants for LOU064 and 20 for placebo. Safety counts at risk are different again, and secondary outcome counts also vary. The registry does not explain all these differences. They may reflect different analysis populations or available measurements, but the record does not establish the reason.

The record does not report the original sample-size justification, a full account of missing-data handling, interim analyses, or a multiplicity plan. It provides only limited detail for reproducing the Bayesian model, including no complete model specification or diagnostics. These gaps constrain independent evaluation of the sponsor’s analysis and sensitivity to its assumptions.

The treatment period was 12 weeks, so the posted results describe a limited observation period. The safety data are counts, and the record does not include listed serious adverse event terms. The posted outcomes and analyses also cover multiple measures, but not every planned analysis can be verified from the registry record. These limitations warrant restraint when generalizing beyond the analyzed participants and study conditions.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Study of Efficacy and Safety of LOU064 in Inadequately Controlled Asthma Patients — NCT03944707.
• Registry record last updated 2021-10-11; status last verified 2021-10.
• Results first posted 2021-04-27.
• 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

NCT03944707 is a randomized, parallel-group, quadruple-masked phase 2 study of LOU064 versus placebo in inadequately controlled asthma. The registry lists enrollment of 76, a 3:2 allocation, and a 12-week treatment period alongside standard background therapy. The study is marked terminated; the reason is not reported in the registry record.

The primary endpoint was change from baseline in pre-dose FEV1 at Week 12. The sponsor’s Bayesian repeated-measures analysis reported a net mean difference of 0.030 liters, with an 80% interval from -0.060 to 0.119. A simple unadjusted recalculation differs in its uncertainty summary, and the sponsor’s analysis takes precedence. Secondary outcomes and descriptive safety counts are also posted, but interpretation is limited by unreported multiplicity and missing-data details, varying participant counts, and the absence of a reported original sample-size justification.