Nebulized Hypertonic Saline for Inpatient Use in COPD: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Nebulized Hypertonic Saline for Inpatient Use in COPD (NCT02266875), a randomized phase 4 study. The primary outcome is Change in Patient-Reported Breathing Difficulty - Using Modified Borg Dyspnea Scale.

2. Clinical Question

3. Trial Design

The registry identifies this as a phase 4, randomized, single-masked, parallel-group trial sponsored by OhioHealth. It records an enrollment of 70 and a completed status. The recorded start is 2014-10, and primary completion is listed as 2017-01-30. The condition of interest is chronic obstructive pulmonary disease. These design labels describe the registered study; additional operational details, including the identity of the masked party, are not reported in the registry record.

Participants were assigned to one of two treatment groups. Both groups received standard 2.5 mg. albuterol treatments once every 6 hours over 24 hours, with as-needed use allowed. The groups differed in the saline used for nebulization: hypertonic saline at 3% or standard saline at 0.9%. The planned assessment described for the primary outcome was before treatment and at completion of the 24-hour period. The registry does not report adherence, the number of treatments actually received, or whether participants deviated from the scheduled regimen.

The primary endpoint was change in patient-reported breathing difficulty on the Modified Borg Dyspnea Scale. The posted group summaries include 29 participants in the hypertonic-saline arm and 30 in the standard-saline arm. The registry also lists 30-day readmission and 30-day all-cause mortality as secondary outcomes. It posts readmission counts, but the mortality outcome result is not reported in the registry record.

Further detail about the randomization procedure, allocation concealment, masking procedures, eligibility rules, analysis populations, and the trial’s original sample-size justification is not reported in the registry record. The registered design supports a comparison between the two assigned saline regimens; it does not, by itself, establish how faithfully the treatment schedule was implemented or how missing outcome data were handled.

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:

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 in Patient-Reported Breathing Difficulty - Using Modified Borg Dyspnea Scale, measured over Pre-treatment (baseline) vs. 24 hours post-treatment.

The primary endpoint measures change in patient-reported breathing difficulty from pretreatment baseline to 24 hours after treatment. The instrument is the Modified Borg Dyspnea Scale, expressed in units on a scale. Its range is 0 to 10: 0 indicates no difficulty breathing, and 10 indicates maximal difficulty in breathing. Participants may report whole numbers and may also report 0.5, described as very, very slight, just noticeable difficulty in breathing.

Change is interpreted directionally. A negative change indicates a reduction in reported breathing difficulty, and a more negative change indicates a greater reduction. The endpoint therefore captures the participant’s own rating rather than an objective lung-function measurement. It is relevant to the trial’s stated question because the comparison concerns reported dyspnea during the 24-hour treatment period.

Change scores also connect the end-of-period assessment to each participant’s pretreatment score, rather than treating the 24-hour score alone as the outcome. General: a change measure can describe how a participant’s recorded status moves over a defined interval, but the interpretation depends on the scale, assessment timing, and completeness of the measurements. The registry does not report a threshold for a clinically important change, nor does it provide additional validation or measurement details beyond the scale description. Thus, the reported means describe the average change in this scale; they do not by themselves establish how noticeable a particular difference would be to patients.

7. Results Posted in the Registry

• Hypertonic Saline: mean -1.40 versus -1.00 on control; difference -0.40 (95% CI -1.35 to 0.55), standardized effect d = -0.21; z-test p = 0.410.

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.

30 Day Readmission

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Hypertonic Saline: 10.3% (3/29) versus 10.0% (3/30) on control; risk difference 0.3 percentage points (95% CI -15.1 to 15.8), risk ratio 1.03 (0.23–4.71); unadjusted two-proportion z-test p = 0.965.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Hypertonic Saline and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists 30-day readmission and 30-day all-cause mortality as secondary outcomes. The posted readmission counts are similar across the two treatment groups, and the registry’s exact test does not indicate a clear separation. The all-cause mortality outcome result is not reported in the registry record. Thus, the overall secondary-outcome picture is incomplete: the available readmission result does not add a clearly distinct pattern to the primary comparison, and the mortality listing cannot be interpreted as a comparative outcome result without its endpoint data.

Secondary outcomes can help describe aspects of the trial beyond the primary measure, but they are not interchangeable with the primary endpoint. Readmission and mortality concern different events and follow-up from the 24-hour dyspnea change. Their findings therefore do not directly validate or overturn the primary comparison. In particular, lack of a clearly separated secondary result is not proof that the groups are equivalent on that outcome.

Unadjusted secondary results carry less weight when multiple outcomes are examined without a stated plan for controlling multiplicity. The registry does not report whether multiplicity adjustment was planned or applied. General: examining several outcomes increases the opportunity for chance findings, so isolated secondary results are usually interpreted as exploratory unless they were prespecified and analyzed under a clear plan. Here, the registry does not supply enough analysis detail to establish that status.

The secondary results should therefore be read as limited contextual information rather than decisive evidence about the treatment contrast. The readmission data are one component of the posted record; the missing mortality result and absent multiplicity details constrain broader conclusions. No composite interpretation across these outcomes is reported in the registry record.

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

• 30 Day Readmission
• 30 Day All Cause Mortality

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous: it is a numerical change score, summarized as a mean and standard deviation in each arm. A mean describes the arithmetic average of the observed scores, while a standard deviation describes how dispersed those scores are around the mean. The posted means are -1.4 for hypertonic saline and -1.0 for standard saline. The corresponding standard deviations are 1.6 and 2.1. These summaries describe the observed change scores; they do not show the full distribution or reveal whether scores were skewed or clustered.

What does the mean difference represent?

The re-calculated mean difference compares the two posted arm means, with hypertonic saline contrasted against standard saline. Its estimate is -0.4 units. Given the endpoint’s direction, a negative contrast means the average change was more negative in the hypertonic-saline group. This is a descriptive contrast in the recorded data, not proof that the treatment caused a difference. Random assignment supports a comparison between groups, but the interpretation still depends on the quality and completeness of trial conduct and outcome recording, details that are not fully reported in the registry record.

The re-calculation is unadjusted and uses the posted summary statistics. It is not an adjusted model controlling for participant characteristics or other variables. The registry does not report an adjusted primary estimate. General: adjustment can account for prespecified covariates, but it can also change an estimate and its uncertainty; without a recorded analysis plan and model details, an adjusted result should not be inferred.

How should the test and p-values be understood?

The registry reports a two-sided t-test for the primary comparison and gives p = 0.320. A two-sided test evaluates departures in either direction rather than testing only whether one specified group has a larger change. The unadjusted re-calculation gives p = 0.41. A p-value describes how unusual data at least as incompatible with a specified null model would be if that model and the test assumptions held. It is not the chance that the treatment has no effect, and it does not measure the probability that the result will replicate.

The test assumes a suitable basis for comparing group means. General: t-based methods are commonly used for mean comparisons, with their performance depending on factors such as the distribution of the data and the adequacy of the standard-error calculation. The registry does not report diagnostic checks, a particular variance assumption, or a model specification beyond the t-test label. The re-calculation uses the reported group sizes and standard deviations and is a simple unadjusted comparison.

What does the confidence interval add?

A confidence interval gives a range of effect estimates compatible with the observed data under the method’s assumptions. For the re-calculated mean difference, the interval includes zero and extends in both directions. This indicates that the data are compatible with no mean difference as well as with differences in either direction. The interval is not a guarantee that the true effect lies within its bounds, and it does not express the probability that any specific value is true. Its width communicates the limited precision of the estimate.

General: confidence intervals reflect both the observed variability and the amount of information available. Greater variability or fewer observations generally leads to less precision, all else being equal. The posted outcome counts are 29 and 30, and the group standard deviations are 1.6 and 2.1. The registry does not provide participant-level results that would permit other checks of distributional shape or subgroup variation.

Why does over-dispersion matter for count or binary outcomes?

The primary endpoint is continuous, so over-dispersion is not the central issue for its reported mean comparison. General: for count data, over-dispersion means the observed variation is greater than assumed by a model; if ignored, standard errors can be too small and intervals or tests can look more certain than warranted. For binary outcomes, analysts need methods suited to event counts and group sizes. The secondary readmission outcome is binary, and the registry reports a Fisher Exact test. It does not report a model-based dispersion assessment.

For readmission, the registry’s reported test is Fisher Exact, with p > 0.999. This method compares the distribution of event and non-event counts between the groups under its assumptions. The posted event counts are small, making an exact test a plausible descriptive choice, but the registry does not state why that test was selected. A non-small p-value should not be interpreted as proof that the groups are equivalent.

What do the planning estimates mean?

The planning estimates are illustrative calculations based on the observed effects, not the original design assumptions. They use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is expressed as a stated fraction of the observed effect. For the continuous outcome, the estimates are participants per arm; for time-to-event outcomes, the stated convention would be total events, though no time-to-event outcome is listed among these posted outcomes. These calculations describe hypothetical future study sizes under the stated assumptions. They are not observed power and do not provide a retrospective probability that this trial detected an effect.

The registry does not report the original sample-size justification or whether the trial had interim analyses. It also does not report a multiplicity plan, detailed missing-data procedures, or the definition of the primary analysis population. Those omissions matter because the planned test, outcome availability, and handling of multiple comparisons can affect how a result should be interpreted. No unreported protocol detail should be inferred from the calculations or test labels.

11. Confidence Intervals and Precision

The re-calculated primary mean difference is -0.4 units, and its confidence interval extends from a negative value to a positive value. Because zero lies within that interval, the data are compatible with no difference as well as with possible differences in either direction. The interval does not establish that the groups are identical; it shows that the observed data do not estimate the contrast with enough precision to exclude zero under the calculation’s assumptions.

The scale is measured in units of patient-reported breathing difficulty. The registry defines the direction of change but does not report a threshold for a clinically important between-group difference. Consequently, the estimate and its interval can be described statistically, but the registry alone does not determine whether any particular value would be meaningful to patients. The mean difference also summarizes groups and cannot describe the range of individual changes.

Observed primary outcome counts were 29 and 30, and the standard deviations were 1.6 and 2.1. These summaries provide context for the amount of data and variability behind the comparison. General: confidence intervals tend to be wider when data are more variable or less abundant, and narrower when information is more precise. An interval that crosses zero is not evidence of equivalence; demonstrating equivalence would require an appropriate margin and analysis, neither of which is reported in the registry record.

For readmission, the registry reports a risk-difference interval that also spans both negative and positive values. That uncertainty limits conclusions about the size and direction of a group difference in that secondary outcome. The mortality outcome result is not reported in the registry record. In both cases, absence of a clearly precise estimate should be distinguished from evidence that no difference exists.

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 estimates describe hypothetical future enrollment under stated assumptions. For the continuous primary outcome and the binary readmission outcome, the figures are participants per arm, not total participants. The planning convention also states that time-to-event calculations would give total events, but no time-to-event outcome is listed among the posted outcomes. The original trial’s own sample-size assumptions and justification are not reported in the registry record.

The calculations use the observed effect as a starting point, with scenarios for 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect. They assume a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The stated effect to detect is the selected fraction of the observed effect. These are planning assumptions for an illustration, not a claim about how the original trial was designed.

The 80% power column gives the estimated number of participants per arm under which the assumed design would have an 80% probability of detecting the specified effect if that effect were real and the assumptions held. The 90% power column uses a higher target probability and consequently calls for more participants under the same general setup. Smaller effects are harder to distinguish from random variation, so planning to detect a smaller fraction of the observed effect requires more participants.

For the primary outcome, the displayed estimates increase as the assumed effect fraction becomes smaller. The same pattern appears in the readmission planning illustration. The estimates are highly dependent on the observed effect, which itself is uncertain, especially when based on a small trial. These values are not observed power: they are prospective planning illustrations and do not tell whether the completed trial had a particular probability of success after its results were known.

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 = -0.400; pooled standard deviation σ = 1.871.
2. n = 2 × (1.96 + 0.842)² × 1.871² / -0.400² = 343.5, rounded up to 344 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 <- -0.4                      # observed difference in means
sigma <- 1.87115688016143                     # 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(2266875)
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 = 344 (80% power), 460 (90% power)
 75% of observed effect: n per arm = 611 (80% power), 818 (90% power)
 50% of observed effect: n per arm = 1,375 (80% power), 1,840 (90% power)
power.t.test: 344.5 
Simulated power at n = 344 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. Analyses Reported by the Sponsor

The registry reports the sponsor’s primary analysis as a two-sided t-test with p = 0.320. The unadjusted re-calculation from the posted group means, standard deviations, and outcome counts gives a mean difference of -0.4 units and p = 0.41. The two p-values differ, so they should be identified as results from distinct analyses rather than blended into a single value.

The sponsor-reported test is the registered result and should be the principal reference for what the registry says was analyzed. The re-calculation is a straightforward comparison of posted summary statistics. The registry record does not give further detail about the sponsor test’s exact implementation, so the reason for the p-value difference is not reported in the registry record. There is no basis in the record to attribute the difference to a specific modeling choice, missing-data method, or adjustment.

The estimate and confidence interval from the re-calculation are useful for describing the direction and uncertainty implied by the summaries, but they do not substitute for a more detailed sponsor analysis. Neither p-value alone determines clinical importance, and both must be read with the observed means, the endpoint’s direction, and the precision of the estimated contrast. The re-calculation is not an independent confirmation using participant-level data.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists a primary endpoint and secondary outcomes, but a detailed strategy for handling multiple comparisons is not reported in the registry record. It is therefore unknown whether the investigators specified a hierarchy, adjusted significance thresholds, or treated secondary analyses as exploratory. General: when several outcomes or comparisons are tested, the chance of at least one apparently unusual result can increase. Adjustment methods can address that issue, but the appropriate approach depends on the questions and analysis plan set before results are examined.

The registry record also does not report the primary analysis population definition. It does not say whether the main analysis was based on all randomized participants, participants who received treatment, participants with complete outcome data, or another group. The recorded enrollment is 70, while the posted primary outcome arm counts are 29 and 30. These figures identify a difference between enrollment and the number represented in the posted endpoint summaries, but the reasons for that difference are not reported in the registry record. It would be inappropriate to infer whether it reflects missing measurements, exclusions, withdrawals, or another cause.

Details of missing-data handling are not reported in the registry record. The record does not specify whether missing values were imputed, excluded, or handled using another method, nor does it give a sensitivity analysis for missing outcomes. General: when outcome availability differs from the intended analysis population, estimates may depend on why data are missing and how those observations are handled. Without those details, the extent to which missingness could affect the comparison cannot be assessed.

The registry does not report interim analyses, stopping rules, or a formal plan for monitoring results. It also does not report the original sample-size justification. These are unknown features, not evidence that a particular procedure was or was not used. The available test labels and planning illustrations do not establish the protocol’s complete statistical plan.

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 0% reporting threshold.

The registry’s adverse-event summary lists 29 participants at risk in the hypertonic-saline group and 30 in the standard-saline group. It records zero serious adverse events in each group, zero other adverse events in each group, and zero deaths in each group in that adverse-event summary. No serious adverse-event terms are listed.

These are counts within the registry’s adverse-event reporting. They should not be read as proof that no adverse events of any kind could occur or that the regimens have established safety. The counts are limited to the participants and reporting scope recorded for this trial. The registry does not provide further detail about event definitions, collection procedures, follow-up completeness, or whether the adverse-event summary corresponds to every participant enrolled.

The zero death counts in the adverse-event summary do not supply the missing comparative result for the separately listed 30-day all-cause mortality secondary outcome. A safety-event summary and a defined secondary efficacy or clinical outcome may have distinct reporting contexts. The mortality endpoint result is not reported in the registry record, so the adverse-event entries should not be used to fill in that missing endpoint analysis.

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

The primary outcome summaries show negative average changes in both groups on a scale where a negative change means reduced patient-reported breathing difficulty. The unadjusted re-calculation estimates a small difference in the direction of a more negative mean change in the hypertonic-saline group, but its confidence interval includes zero and extends in both directions. The registry’s own two-sided test reports p = 0.320. Taken together, these data do not provide a precise estimate of the between-group difference.

That statistical description is not a conclusion that the treatments are equivalent, and it is not a determination that either treatment works or does not work. The trial compared two saline concentrations within a regimen that included albuterol in both groups. It does not answer what would happen without albuterol, with a different schedule, or in a population not represented by the enrolled participants. The registry does not report a threshold for a clinically important difference on the scale, so statistical estimates cannot be translated into a definitive judgment about patient importance from the record alone.

The available secondary information is also limited. Readmission results do not show a clear separation between groups, while the listed 30-day mortality result is not reported in the registry record. The adverse-event summary records no serious or other adverse events and no deaths in the listed groups, but these counts do not establish safety beyond the scope and follow-up recorded.

Interpretation is further constrained by missing analysis details. The registry does not report the original sample-size rationale, interim analyses, the primary analysis population, missing-data methods, or a multiplicity plan. Those omissions do not invalidate the posted results, but they limit how fully readers can assess their robustness and intended inferential scope. The most defensible reading is therefore descriptive and cautious: the registry records the observed group summaries and test, while the magnitude and precision of any comparative effect remain uncertain.

18. Why This Trial Matters Statistically

This trial illustrates why a reported group difference should be read together with its uncertainty. The primary means move in the same negative direction, and the estimated between-group contrast is not enough on its own to establish a clear separation. The confidence interval includes values on either side of zero, so the point estimate should not be mistaken for a precise or definitive effect.

It also demonstrates the distinction between a sponsor-reported analysis and a re-calculation from summary statistics. The registry reports a two-sided t-test, while an unadjusted re-calculation yields a different p-value. Keeping those analyses distinct is important: the re-calculation helps readers understand what follows from the posted means and standard deviations, but it cannot recreate unreported details of the sponsor’s analysis or replace participant-level analysis.

The planning illustrations show another important principle. Sample-size estimates depend on the effect chosen for detection and on assumptions about allocation, significance level, and calculation method. A trial’s observed estimate is itself uncertain, so planning from it should be treated as an illustration rather than a guarantee about a future study. The original study’s design assumptions are not reported in the registry record.

Finally, registry outcomes are not always equally complete. The primary endpoint and readmission results have posted data, while the mortality result is not reported. Missing analysis-population, missing-data, and multiplicity details further shape the limits of interpretation. Statistical literacy involves identifying both what the data describe and what the record leaves unresolved.

19. Limitations

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

The primary endpoint summaries include 29 participants in the hypertonic-saline group and 30 in the standard-saline group, compared with an enrollment of 70. The registry does not explain the difference between enrollment and the endpoint counts. Without a participant flow account, reasons for absent endpoint data cannot be determined, and the potential influence of missing measurements cannot be assessed.

The registry does not report the original sample-size justification, a detailed statistical analysis plan, or whether interim analyses took place. It also does not define the primary analysis population or describe missing-data procedures. Those omissions limit assessment of whether the posted analysis followed a prespecified plan and how sensitive the findings may be to outcome availability.

Further design details are not reported in the registry record, including the allocation procedure, concealment procedures, identity of the masked party, eligibility criteria, adherence, and actual use of as-needed treatments. These details matter for assessing conduct and the interpretation of a randomized comparison, but their absence from the registry is not evidence of a particular problem.

The primary measure is patient-reported, and the registry does not report a clinically important change threshold. The posted means and standard deviations do not reveal the full distribution of scores or participant-level variation. The registry also does not report the result for the listed 30-day all-cause mortality outcome. Finally, no multiplicity strategy is reported for the secondary outcomes. These limits counsel against extending the findings beyond the specific 24-hour comparison and outcomes recorded.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Nebulized Hypertonic Saline for Inpatient Use in COPD — NCT02266875.
• Registry record last updated 2017-11-22; status last verified 2017-10.
• Results first posted 2017-11-22.
• 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.

23. Record Summary

The registry describes a completed, phase 4, randomized, single-masked, parallel-group trial sponsored by OhioHealth, with enrollment of 70. It compared nebulized hypertonic saline at 3% with standard saline at 0.9%; both groups received standard 2.5 mg. albuterol on an every-6-hours schedule for 24 hours, with as-needed use allowed.

The primary endpoint was change in Modified Borg Dyspnea Scale score from pretreatment baseline to 24 hours. Posted mean changes were -1.4 and -1.0, respectively. The registry reports a two-sided t-test with p = 0.320; an unadjusted re-calculation gives a mean difference of -0.4 and p = 0.41, with an interval spanning zero. The record lists 30-day readmission and 30-day all-cause mortality as secondary outcomes; the mortality result is not reported in the registry record.

The registry records zero serious adverse events, zero other adverse events, and zero deaths in each adverse-event group. Important details, including missing-data handling, analysis populations, multiplicity procedures, interim analyses, and the original sample-size justification, are not reported in the registry record.