Effect of Postsurgical Systemic Doxycycline After Regenerative Periodontal Therapy: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Effect of Postsurgical Systemic Doxycycline After Regenerative Periodontal Therapy (NCT01030666), a randomized phase 4 study. The primary outcome is Vertical Clinical Attachment (PAL-V) Gain 6 Months After Surgery.

2. Clinical Question

The clinical question is a comparison between treatment groups, not a test of whether either group improved from its own baseline. Both groups received regenerative therapy; the contrast concerns the additional postoperative doxycycline course versus placebo. The primary posted outcome is a continuous measurement in millimetres. The registry also lists radiographic bony fill at 12 months as a secondary outcome. The outcome record does not report results for the hypothesis about flap dehiscence or defect exposure.

3. Trial Design

The registry identifies a randomized, parallel-group, quadruple-masked, phase 4 clinical trial comparing doxycycline with placebo after regenerative periodontal therapy. The condition listed is periodontitis. The registry lists Peter Eickholz as sponsor. Recruitment began in 2007-04, primary completion was recorded as 2011-01, and the current status is terminated. The reason for termination is not reported in the registry record.

The registry records enrollment of 61. Its study summary describes an intended study in which one infrabony defect in each of 90 patients would receive regenerative treatment. The posted primary-outcome summaries use a per-protocol population of participants who attended the six-month re-examination. The reported group sizes for that outcome are 27 in the doxycycline group and 31 in the placebo group. These outcome counts should not be treated as a replacement for the enrollment figure: they describe the participants contributing to that specific result.

The treatment descriptions pair the study medication with regenerative periodontal care, including a modified or simplified papilla preservation flap, scaling, and Prefgel/Emdogain. Both groups are also listed with 0.12% chlorhexidine gluconate solution; ibuprofen 400 mg and 1% chlorhexidine gluconate gel are described as needed. The registry does not report further detail on how masking was implemented or assessed. It also does not report the reason the trial ended as terminated, or whether the planned enrollment changed during conduct.

Measurements described in the summary include clinical indices and standardized radiographs before surgery and at follow-up. The posted primary comparison concerns vertical clinical attachment gain at 6 months; the secondary comparison concerns radiographic bony fill at 12 months. A full protocol, the trial’s original statistical analysis plan, and the trial’s own sample-size assumptions 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: per protocol analysis: all participants who attended the 6 months re-examination

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 Vertical Clinical Attachment (PAL-V) Gain 6 Months After Surgery, measured over Baseline to 6 months after surgery.

The primary endpoint is mean vertical clinical attachment gain from baseline to 6 months after surgery, measured in millimetres. The registry describes the outcome as the difference between the baseline and six-month PAL-V measurements. The study hypothesis also refers to CAL-V. Both labels concern vertical clinical attachment, but the record does not explain the variation in abbreviation.

Measurements were made to the nearest 0.5 mm using a straight manual periodontal probe. The cemento-enamel junction served as the reference point; if it was destroyed by a restoration, the restoration margin served as the reference. The endpoint therefore represents a clinical measurement of attachment level at the treated site, expressed as change over the stated follow-up interval. A positive gain is the outcome named by the registry, but a group mean alone does not show how outcomes varied among individuals.

A continuous endpoint retains the magnitude of measured change rather than reducing participants to categories such as improved or not improved. Comparing group means can estimate the average difference between treatment strategies, while the standard deviations describe the spread of measurements within each group. That makes the endpoint useful for assessing the size and precision of the between-group contrast. It does not, by itself, establish why any observed change occurred or whether a difference is clinically important. The registry record does not report a threshold for clinical importance.

7. Results Posted in the Registry

• Doxycycline: mean 3.11 versus 3.40 on control; difference -0.29 (95% CI -1.14 to 0.56), standardized effect d = -0.17; z-test p = 0.502.

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.

Radiographic Bony Fill 12 Months After Surgery (Reduction of Distance Cemento-enamel Junction [CEJ] to Bony Defect [BD])

• 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:
  • Doxycycline: mean 1.09 versus 1.51 on control; difference -0.42 (95% CI -1.90 to 1.06), standardized effect d = -0.15; z-test p = 0.578.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Doxycycline and the control. The interval gives the range of effects that remain compatible with the data.

The registry posts one secondary endpoint: radiographic bony fill at 12 months, measured as reduction in the distance from the cemento-enamel junction to the bony defect. Its group means and unadjusted contrast show the same broad inferential pattern as the primary outcome: the point estimate is negative under the doxycycline-minus-placebo ordering, while the confidence interval includes zero and the unadjusted p-value does not distinguish the contrast from zero. The uncertainty is substantial, so the direction and size of the average difference remain unclear.

This secondary result is related to the primary question because both outcomes assess aspects of the regenerative treatment result, but they are different measurements at different follow-up times. A radiographic measure of bony fill is not interchangeable with clinical vertical attachment gain. Similar uncertainty across the two endpoints does not establish that the underlying treatment effects are the same, nor does it independently confirm the primary result.

Secondary findings generally carry less weight when they are unadjusted and are considered alongside a primary outcome and other possible outcomes. If multiple hypotheses are tested without a strategy for controlling multiplicity, the chance of obtaining apparently notable results among the set can increase. The registry does not report a multiplicity adjustment or a prespecified testing hierarchy. In this record, the posted secondary comparison is not statistically distinct from zero in its unadjusted analysis; it should be treated as supportive descriptive context, not as a separate confirmatory conclusion.

The registry summary also mentions bony fill and postoperative flap dehiscence or defect exposure in the study hypothesis, but the posted outcome results include only the listed secondary radiographic measure. Results for dehiscence and defect exposure are not reported in the registry record. The absence of posted results for those outcomes cannot be interpreted as evidence that no such events occurred or that the hypothesis was confirmed or refuted.

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

• Radiographic Bony Fill 12 Months After Surgery (Reduction of Distance Cemento-enamel Junction [CEJ] to Bony Defect [BD])

9. Statistical Interpretation

10. Statistical Methods Explained

The posted outcomes are continuous measurements summarized by group means and standard deviations. A mean describes the arithmetic average of the measured gains within a group. A standard deviation describes the degree to which individual measurements vary around that mean; it is not the same as the uncertainty in the estimated mean. The outcome counts indicate how many participants contributed to each specific summary.

What does the mean difference represent?

The mean difference compares the doxycycline group with the placebo group by subtracting the placebo mean from the doxycycline mean. For the primary outcome, the posted estimate is -0.29 mm. The negative sign indicates that the doxycycline group mean was lower under this ordering. It does not indicate a probability, nor does it account for whether the difference is clinically important. A group mean comparison also does not describe every participant’s response.

The secondary outcome uses the same kind of contrast: the posted mean difference is -0.42 mm for radiographic bony fill. Both estimates are unadjusted comparisons of group summaries. The registry record does not report a model adjusting for baseline measurements or other variables, so the results should not be described as adjusted effects.

What does a confidence interval add?

In general, a confidence interval expresses uncertainty about an estimated quantity under the assumptions of the statistical method. It gives a range of values compatible with the observed data and method; it is not a range containing a stated proportion of individual participant outcomes. For a difference between means, an interval that includes zero indicates that a zero average difference is among the values compatible with the data at the interval’s confidence level. It does not establish that the true difference is zero.

The primary interval crosses zero and extends in both directions, as does the secondary interval. That pattern is consistent with uncertainty about the direction as well as the magnitude of the average contrasts. A confidence interval should be read alongside the point estimate, the outcome scale, and the clinical context. The registry record does not report a minimum clinically important difference with which to judge the intervals.

How should the p-values be read?

The unadjusted p-values are 0.502 for the primary outcome and 0.578 for the secondary outcome. In general, a p-value measures how incompatible the observed data are with a specified null model, assuming the model and analysis conditions hold. It is not the probability that the null hypothesis is true, and it is not the probability that a result arose by chance. A p-value does not measure the size or importance of a difference. Here, both p-values accompany intervals that include zero, so neither comparison gives a clear statistical distinction from a zero mean difference under the unadjusted method.

The record does not report the trial’s formal analysis plan or sponsor-conducted tests. The estimates and p-values posted alongside the summary statistics are simple unadjusted recalculations. They should not be confused with a prespecified adjusted analysis. If the registry record had a discrepancy between sponsor-reported and recalculated results, the sponsor’s analysis would take precedence; no discrepancy is flagged for these results.

Why can spread and over-dispersion matter?

In general, larger variation within groups makes a mean difference harder to estimate precisely, particularly when outcome groups are small. Over-dispersion refers to variability greater than a statistical model assumes. When present and ignored, it can make standard errors too small and confidence intervals too narrow, giving an overly certain impression. The posted standard deviations indicate appreciable variation in these measurements, but the registry does not report a formal assessment of over-dispersion or a model that accounts for it. No conclusion about a specific variance problem should be inferred from the summaries alone.

The group standard deviations are 1.5 mm and 1.79 mm for the primary outcome, and 2.7 mm and 2.89 mm for the secondary outcome. These describe observed spread; they are not treatment-effect estimates. The fact that variation is large relative to the observed contrasts helps explain why the estimates are imprecise. It does not establish whether the variation reflects measurement error, differences among participants, or other sources.

What does the analysis population imply?

The primary outcome is identified as a per-protocol analysis among participants who attended the six-month re-examination. In general, a per-protocol population focuses on participants meeting specified study conditions, whereas an intention-to-treat analysis retains participants according to randomized assignment. The registry record does not report an intention-to-treat result or the detailed rules used to define per-protocol eligibility. Attendance-based inclusion can limit how well a result represents everyone randomized if attendees differ from those without follow-up measurements.

The different outcome counts across follow-up points show that the posted summaries use different numbers of measurements for each endpoint. The registry does not report reasons for unavailable measurements, imputation procedures, or sensitivity analyses. Therefore, the possible influence of missing data cannot be quantified from the record.

11. Confidence Intervals and Precision

Precision is about how narrowly the data estimate the between-group contrast. The primary mean difference is -0.29 mm, but its confidence interval crosses zero and includes values in both directions. This means that the posted data are compatible with the observed estimate and with a range of other possible average differences. The interval does not establish that the groups are identical, and the record does not specify a threshold that would separate clinically important from unimportant differences.

The secondary mean difference is -0.42 mm, with a confidence interval from -1.9 to 1.06 mm. This interval includes zero and is wide relative to the point estimate. It permits uncertainty about both the direction and size of the average contrast. The secondary result therefore offers limited precision about the actual between-group difference.

In general, confidence intervals tend to be wider when the outcome is variable or when the amount of information is limited. The posted standard deviations are large relative to the observed contrasts, and the outcome groups are modest in size. Both features are consistent with the uncertainty reflected in the intervals. The record does not report a precision target, a clinically important difference, or an original sample-size justification, so it is not possible to determine from the registry alone whether the trial was designed to estimate a clinically meaningful contrast precisely.

Neither interval should be interpreted as a prediction interval for individual outcomes. The intervals concern the estimated group mean difference under the calculation method. They also do not resolve potential issues related to missing observations, selection into the per-protocol population, or unreported analysis choices. Precision is a property of the estimate in relation to its uncertainty, not a verdict on the treatments.

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 are illustrative calculations based on the observed effect, not the trial’s original design assumptions. For these continuous outcomes, the figures are participants per arm, not total events. The calculation assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. The trial’s own original sample-size assumptions are not reported in the registry record.

The 80% power column describes the estimated participants per arm for a hypothetical study that would have an 80% chance of detecting the specified effect under the planning assumptions, if that effect and the assumptions were correct. The 90% column describes the corresponding planning target for a 90% chance. These are design illustrations, not guarantees. For the primary outcome, the estimates range from 516 participants per arm for planning at 100% of the observed effect to 2,062 participants per arm for 50% of that effect at the 80% target; the corresponding 90% figures range from 690 to 2,760. Planning for 75% of the observed effect gives intermediate figures.

The secondary endpoint has its own planning estimates: at 80% power, 701 participants per arm for 100% of the observed effect and 2,802 for 50%; at 90% power, the corresponding values are 938 and 3,751. Planning for 75% again falls between those values. Smaller effects require more participants because they are harder to distinguish from random variation under the same assumptions. These calculations are not observed power.

The observed effects used in these illustrations come from the posted comparisons and may be unstable, especially when estimates are imprecise. A planning calculation should not be read as evidence that a future study will achieve the stated power if its true effect, variability, allocation, or analysis differs from the assumptions. The registry’s planned study description refers to 90 patients, while the actual enrollment is recorded as 61; the reason for that difference is not reported in the registry record.

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 = -0.290; pooled standard deviation σ = 1.662.
2. n = 2 × (1.96 + 0.842)² × 1.662² / -0.290² = 515.4, rounded up to 516 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 <- -0.29                      # observed difference in means
sigma <- 1.66166332329988                     # 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(1030666)
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 = 516 (80% power), 690 (90% power)
 75% of observed effect: n per arm = 917 (80% power), 1,227 (90% power)
 50% of observed effect: n per arm = 2,062 (80% power), 2,760 (90% power)
power.t.test: 516.3 
Simulated power at n = 516 per arm: 0.798 (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 whether the investigators adjusted for testing multiple outcomes, used a prespecified testing hierarchy, or defined how secondary outcomes would be interpreted alongside the primary outcome. The posted p-values are unadjusted. In general, multiplicity matters because testing multiple hypotheses can increase the chance of at least one apparently unusual result even when none of the underlying effects is real. Without a stated strategy, the secondary comparison should be treated as exploratory context rather than a stand-alone confirmatory finding.

The registry identifies the primary population as participants who attended the six-month re-examination and describes the analysis as per protocol. It does not report the complete eligibility rules for that population, the number randomized in each arm, or an intention-to-treat analysis. The posted group counts for the primary and secondary outcomes are different, reflecting the measurements contributing to each summary; reasons for the missing measurements are not reported in the registry record.

Methods for handling missing outcomes are also not reported. There is no registry description of imputation, sensitivity analyses, or an assessment of whether missingness differed between groups. In general, missing data can affect a comparison if the participants with available measurements differ systematically from those without them. The summaries alone cannot establish whether this occurred or determine the direction or size of any resulting bias.

The registry record does not report interim analyses, stopping rules, protocol deviations, or a complete statistical analysis plan. The reason for the terminated status is not reported. These omissions prevent a full assessment of whether the analyses followed prespecified procedures or whether study conduct affected the posted estimates. They do not justify assuming that any particular issue occurred; they identify information that is unavailable in the registry record.

The posted comparisons are unadjusted calculations from summary statistics, and the registry reports no formal analyses. The record does not describe adjustment for baseline values or other factors. These limitations make the findings useful as a transparent description of the posted group summaries, but they constrain causal and confirmatory interpretation.

15. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

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

The registry reports zero participants affected by serious adverse events in the doxycycline group among 28 at risk, and zero in the placebo group among 33 at risk. No serious adverse-event terms are listed. The record also reports other adverse events affecting 8 participants among 28 at risk in the doxycycline group and 9 among 33 at risk in the placebo group. These are registry counts; the record does not provide further detail about event types, severity, timing, or whether individual participants experienced more than one event.

These figures should be read as the reported counts for the stated at-risk groups, not as proof that serious events were impossible or that the groups had identical safety profiles. The registry record does not report deaths. It also does not describe how adverse events were collected, whether events were judged related to study medication, or how long safety follow-up continued. The counts therefore provide limited descriptive information and do not establish comparative safety.

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

The posted results describe average outcomes among participants with measurements, and the primary analysis is specifically identified as per protocol among attendees at the six-month re-examination. For that population, the observed mean attachment gains are close, and the estimated between-group difference is uncertain. The secondary radiographic comparison is also uncertain. Neither result establishes a precise average advantage for either assigned strategy, and neither demonstrates equivalence.

A non-significant unadjusted result does not prove that there is no effect. It means that these data, analyzed in this way, do not provide a clear statistical distinction from a zero average difference. The confidence intervals still allow a range of possible effects. Without a clinically important difference specified in the registry, the statistical results cannot determine whether any particular value in that range would matter clinically.

The comparison concerns doxycycline added after regenerative periodontal therapy, not doxycycline as a replacement for that therapy. Both groups are described as receiving regenerative procedures and associated care. The findings should not be generalized automatically to other populations, procedures, dosing schedules, or follow-up periods. The registry record describes the primary outcome at 6 months and radiographic bony fill at 12 months; it does not provide a complete set of results for the other measurements mentioned in the summary.

The results also do not answer the study hypothesis about flap dehiscence and defect exposure, because those outcomes are not reported among the posted endpoint results. Nor do the adverse-event counts establish a comprehensive safety comparison. The trial’s terminated status has no recorded explanation, so it should not be used to infer the reason results are limited or to infer anything about treatment effects.

Overall, the record supports a cautious reading of two imprecise, unadjusted comparisons. It does not support a claim that doxycycline works or does not work, that the treatments are equivalent, or that the observed differences are clinically important. Those judgments would require additional information, including the analysis plan, missing-data methods, a clinically meaningful threshold, and fuller outcome reporting.

17. Why This Trial Matters Statistically

This trial illustrates the distinction between an observed difference and a well-estimated difference. The posted primary means differ by -0.29 mm under the stated group ordering, but the confidence interval crosses zero and the unadjusted p-value is 0.502. The secondary comparison is likewise uncertain. Reading point estimates without their uncertainty could make small differences appear more conclusive than the data justify.

It also highlights why the analysis population matters. The primary result is based on participants who attended the six-month examination, rather than a reported intention-to-treat analysis. Different endpoint counts at different follow-up points make it important to understand which participants contribute to each outcome and how unavailable measurements were handled. That information is not reported in the registry record.

The planning illustrations show how strongly sample-size requirements depend on the effect size chosen for planning. Smaller effects require more participants under the stated assumptions. Because the calculations use observed effects and are not the trial’s original design assumptions, they are not evidence about the trial’s planned power or about whether a future study would reproduce the same effect.

Finally, the record distinguishes posted descriptive results from a formal sponsor analysis: no formal analyses are reported, while the posted comparisons are unadjusted calculations from summary statistics. Missing information about multiplicity, missing data, and the reason for termination limits interpretation. These are general lessons in reading clinical trial records: assess the estimate, its precision, the population analyzed, and the completeness of reporting together.

18. Limitations

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

Several features specific to this record constrain interpretation. The study summary describes a plan involving 90 patients, while enrollment is recorded as 61. The reason for this difference and the reason the study is listed as terminated are not reported in the registry record. No conclusion about recruitment difficulties, early stopping, or any other cause can be drawn from those details alone.

The primary outcome population is per protocol and limited to participants attending the six-month re-examination. The registry does not report the full per-protocol rules or an intention-to-treat analysis. The available counts differ between the primary and secondary outcomes, but the reasons for missing measurements and the approach to missing data are not reported. These omissions leave uncertainty about how representative the analyzed participants are of everyone enrolled or assigned.

The outcome summaries provide means and standard deviations, with unadjusted recalculated comparisons, but the registry reports no formal analyses. A statistical analysis plan, adjustment strategy, and multiplicity procedure are not reported. The record also does not state a clinically important threshold for attachment gain or bony fill, so statistical uncertainty cannot be translated into a judgment about clinical importance.

The registry lists a hypothesis concerning flap dehiscence and defect exposure, but does not post results for those outcomes. It records adverse-event counts without descriptions of event types or relatedness, and deaths are not reported. The reason for termination, interim analyses, and stopping rules are also not reported. These gaps limit the scope of conclusions, while not establishing that any particular bias, safety issue, or protocol departure occurred.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Effect of Postsurgical Systemic Doxycycline After Regenerative Periodontal Therapy — NCT01030666.
• Registry record last updated 2016-11-03; status last verified 2016-09.
• Results first posted 2012-11-27.
• 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.

22. Record Summary

The registry describes a randomized, parallel, quadruple-masked, phase 4 comparison of doxycycline and placebo after regenerative periodontal therapy for infrabony defects. It records enrollment of 61, primary completion in 2011-01, and terminated status. The reason for termination is not reported in the registry record.

The primary posted result is mean vertical clinical attachment gain from baseline to 6 months in the per-protocol population attending re-examination. The doxycycline and placebo means are 3.11 mm and 3.4 mm, with an unadjusted mean difference of -0.29 mm and p = 0.502. The secondary 12-month radiographic bony-fill comparison is also imprecise and unadjusted.

The registry reports no formal analyses. Details about multiplicity, missing-data handling, original sample-size assumptions, and the reason for termination are not reported. The posted comparisons therefore support descriptive, cautious interpretation rather than a definitive conclusion about treatment effect.