Laxative Effectiveness of a Phytotherapeutic Tea: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Laxative Effectiveness of a Phytotherapeutic Tea (NCT00872430), a randomized phase 2 study. The primary outcome is Intestinal Transit Time.

2. Clinical Question

The clinical question is whether intestinal transit time differs between the phytotherapeutic laxative tea and placebo in people with chronic constipation. The registry describes a randomized, placebo-controlled crossover trial. In a crossover design, participants receive each intervention during different periods, so the comparison concerns outcomes under the two interventions rather than a simple comparison of two unrelated groups.

This question is about a measured physiological outcome, not a broad assessment of all effects or risks. The registry also lists a secondary outcome concerning patients with no evacuation after each intervention period. A result on transit time alone cannot establish how the tea affects other outcomes, nor does it describe the experience of every participant.

3. Trial Design

The registry identifies the study as a completed phase 2, randomized, single-masked, placebo-controlled clinical trial. Its model is crossover: participants were assigned to a treatment sequence and received both placebo and laxative tea in different intervention periods. The registry describes the two sequences as placebo first and tea second, or tea first and placebo second. Each sequence included a washout period of 9 days between interventions. Which party or parties were masked is not reported in the registry record.

The listed enrollment is 20. For the primary outcome, the posted summaries report 20 observations for placebo and 20 for laxative tea. In a crossover study, the same participant may contribute an observation under each intervention. Therefore, those two outcome summaries do not imply two unrelated groups, and they should not be added to infer a participant total. The registry record does not explain how missing observations, if any, were handled.

The primary outcome is intestinal transit time, measured in hours. The timeframe is day 3 and day 17, corresponding to the assessment timing across the intervention periods. The description says participants ingested radiopaque markers and had an abdominal x-ray on day 3 of each intervention period. A radiologist unaware of treatment allocation counted the markers remaining in the colon, and a standard formula was used to estimate transit time.

The registry lists the sponsor as Hospital de Clinicas de Porto Alegre, with study start in 2002-07 and primary completion in 2002-12. The registry record does not report the original sample-size justification, a detailed protocol for sequence or period effects, or the prespecified statistical model for the crossover data. Those omissions limit how fully the posted aggregate results can be interpreted.

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: Twenty patients fulfilled elegibility criteria. No patients were excluded after signing informed consent form and randomization.

First Intervention

Washout Period

Second Intervention

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 Intestinal Transit Time, measured over day 3 and day 17.

Intestinal transit time measures how long material takes to move through the intestine, expressed in hours. In this trial, the registry describes an indirect radiologic measure: participants ingested radiopaque markers, then underwent an abdominal x-ray on day 3 of each intervention period. A radiologist who was unaware of treatment allocation counted the markers still present in the colon. A standard formula, accounting for marker ingestion, timing and the count remaining, was used to estimate transit time. The registry gives the timeframe as day 3 and day 17.

This endpoint is useful for a trial about constipation because it quantifies intestinal movement rather than relying only on a subjective impression. A continuous measure can capture variation across participants and can be summarized with a mean and standard deviation, as in the posted results. Those summaries describe the observed measurements, but they do not by themselves reveal how outcomes varied within the same participant across the two periods.

The measure is not equivalent to a complete assessment of constipation or of the tea’s safety. Transit time is one specific physiological outcome. The registry lists a separate secondary outcome concerning absence of evacuation, but the primary endpoint alone does not address all symptoms, adverse effects, or longer-term outcomes. The registry record does not report additional details about validation or measurement reliability for this specific trial.

7. Results Posted in the Registry

• Laxative Tea: mean 15.66 versus 42.30 on control; difference -26.64 (95% CI -35.94 to -17.34), standardized effect d = -1.78; z-test p = <0.001.

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.

Number of Patients With no Evacuation After Each Intervention Period

• 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:
  • Laxative Tea: 0.0% (0/20) versus 45.0% (9/20) on control; risk difference -45.0 percentage points (95% CI -66.8 to -23.2); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Laxative Tea than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry lists one secondary outcome, concerning the number of patients with no evacuation after each intervention period. Its overall direction is consistent with the primary outcome’s pattern: the posted results favor the tea condition on the recorded outcome. This provides a related, but not interchangeable, perspective. Transit time measures a continuous physiological outcome, while absence of evacuation is a separate outcome with a different scale and interpretation.

Agreement in direction can make the findings look coherent across outcomes, but it does not independently confirm the primary result. The outcomes may be related, and both arise from the same trial and its participants. The secondary comparison also shares the design and reporting limitations of the primary comparison, including incomplete information about crossover analysis, analysis populations and missing data. It should not be treated as an independent replication.

Secondary outcomes are often interpreted with less weight than a primary outcome because they may be less central to the original question and because testing multiple outcomes can increase the chance of a nominally unusual result. In general, multiplicity procedures can adjust interpretation when several hypotheses are tested, but the registry record does not report whether any such procedure was planned or used. The record lists one posted secondary outcome; it does not establish whether other outcomes were considered during the study or analysis.

The secondary result is therefore best read as supportive descriptive context rather than as a decisive additional test. Its relation to the primary endpoint is clinically and statistically relevant, but it cannot resolve uncertainty about the analysis model, precision, or generalizability. The separate outcome should retain its own meaning rather than being collapsed into a single claim about treatment effect.

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

• Number of Patients With no Evacuation After Each Intervention Period

9. Statistical Interpretation

10. Statistical Methods Explained

The posted results combine descriptive summaries with an inferential comparison. The primary outcome is continuous, measured in hours, and reported as a mean with a standard deviation for each intervention. A mean describes the central value of the observed measurements; a standard deviation describes how dispersed those measurements are around the mean. Neither statistic alone conveys the uncertainty in the treatment contrast.

What does the mean difference represent?

The recalculated contrast is defined as laxative tea minus placebo. Its estimate is -26.64 hours. Because the tea mean is lower than the placebo mean, the contrast is negative. The confidence interval, -35.94 to -17.34 hours, describes uncertainty around that estimated difference under the calculation used. The calculation is unadjusted and based on posted summary statistics. It is not a participant-level model of the crossover design.

What does the t-test contribute?

The registry reports a two-sided t-test with p < 0.001 for the primary comparison. In general, a two-sided test evaluates evidence against a null hypothesis of no difference in either direction. A p-value describes how unusual data at least as inconsistent with that null would be under the test’s assumptions; it is not the probability that the null hypothesis is true. The posted p-value indicates strong evidence against no difference under the reported test, but it does not establish the model’s suitability for paired crossover data.

The registry record does not state whether the reported t-test was paired or unpaired, or whether another model was used in the sponsor’s analysis. In general, a paired method uses the within-person difference between intervention periods and can remove some variation attributable to stable participant characteristics. An unpaired method treats the intervention summaries as independent. For a crossover study, the distinction is consequential. A participant-level dataset and a clear analysis description would be needed to assess the model, period effects and sequence effects directly.

Why do variation and distribution matter?

The reported standard deviations are 18.86 hours for placebo and 9.71 hours for tea. In general, the standard deviation indicates observed variability, while the standard error concerns the precision of an estimated quantity. For a mean difference in a crossover trial, the variability of within-person differences is especially relevant. It cannot be recovered from the two marginal standard deviations alone unless the within-person relationship is also known. Consequently, the recalculation from posted summaries cannot fully represent paired-data uncertainty if that relationship is unavailable.

In general, a t-test relies on assumptions about the sampling distribution of the estimate. Strong skew, outliers, dependence not accounted for, or unequal variability can affect how well a test performs. The registry record does not report diagnostic checks, transformations, robust methods, or model adjustments. This does not show that an assumption was violated; it means the record does not allow readers to evaluate those matters.

What is a standardized effect?

The posted recalculation gives a standardized effect, d = -1.776, using a pooled standard deviation of 15.0. In general, standardization expresses a difference relative to a measure of variability, so it can help compare outcomes measured on different scales. It does not replace the hours-scale estimate, and its interpretation depends on the standardization method. Here, it is a recalculated summary, not a substitute for a crossover-specific participant-level estimate.

What can be inferred from the reported analysis?

The sponsor’s reported analysis lists a two-sided t-test and p < 0.001. Its estimate and confidence limits are not reported in the registry record. The posted recalculation supplies an unadjusted mean difference and interval based on the group summaries. Since the record indicates no discrepancy between the reported p-value and the recalculated result, the sponsor’s analysis remains the principal reported analysis; the recalculation is a transparent supplementary reading of the summaries, not a replacement for the sponsor’s method.

More broadly, an inferential result depends on design, measurement, analysis population, missing-data handling and model assumptions. The trial’s randomized crossover design is important because allocation sequence and within-person comparisons can affect the appropriate analysis. The registry record does not report a full statistical analysis plan, handling of period or sequence effects, carryover assessment, interim analyses, or missing-data procedures. Those details should not be inferred from the p-value or from the summary statistics.

11. Confidence Intervals and Precision

The primary mean difference is -26.64 hours, with a 95% confidence interval from -35.94 to -17.34 hours. A confidence interval is an interval produced by a statistical procedure that, under its assumptions and repeated use, would cover the underlying quantity at the stated rate. It is not a statement that there is a 95% probability that this particular interval contains the true effect.

The interval gives a useful sense of precision on the hours scale: the values it spans are all negative, so the posted recalculation is consistent with a lower mean transit time under tea. The interval is not a range containing every participant’s response. Individual outcomes can vary more widely than the uncertainty around a mean contrast, and the standard deviations of 18.86 hours and 9.71 hours describe outcome spread rather than interval precision.

For this crossover trial, the interval’s interpretation depends on how the comparison was calculated. The posted recalculation is unadjusted and based on summary statistics. The record does not report the within-participant covariance, a paired confidence interval, or sufficient details to verify adjustment for period and sequence. In general, exploiting paired observations can change the estimated uncertainty because participants’ two measurements may be correlated. The posted interval therefore should be read as the interval attached to the stated recalculation, rather than assumed to be a fully specified crossover-model interval.

The registry’s own analysis reports p < 0.001 but does not report its estimate or confidence limits. That p-value conveys evidence under the sponsor’s reported test, not the width of an effect interval. The registry record does not report an interval for the sponsor’s analysis, so its precision cannot be compared directly with the recalculated interval.

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 effect, not the trial’s original design calculation. They assume a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The illustrated effect to detect is a stated fraction of the observed effect. The figures are participants per arm for 80% power and participants per arm for 90% power; they are not total event counts. The planning note specifies total events only for time-to-event outcomes, which this continuous endpoint is not.

In plain language, the 80% power column gives the hypothetical participants needed in each arm for an 80% chance of detecting the chosen effect under the stated assumptions, if that effect were the true one. The 90% power column uses a higher detection probability and therefore generally requires more participants for the same effect and assumptions. These values are not observed power and do not describe the probability that the completed trial’s finding is correct.

The planning scenarios use the observed effect as a reference and then consider smaller fractions of it. Smaller effects are harder to distinguish from random variation, so they generally require more participants. These calculations do not establish that the original study was designed for the observed effect, nor do they account for the crossover structure unless explicitly built into the calculation. The registry record does not report the trial’s own sample-size justification or original design assumptions. The planning figures should therefore be read as conditional illustrations rather than as evidence about the design or adequacy of the completed study.

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 = -26.640; pooled standard deviation σ = 15.000.
2. n = 2 × (1.96 + 0.842)² × 15.000² / -26.640² = 5.0, rounded up to 5 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 <- -26.64                      # observed difference in means
sigma <- 14.9997283308732                     # 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(872430)
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 = 5 (80% power), 7 (90% power)
 75% of observed effect: n per arm = 9 (80% power), 12 (90% power)
 50% of observed effect: n per arm = 20 (80% power), 27 (90% power)
power.t.test: 6.1 
Simulated power at n = 5 per arm: 0.695 (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 reported primary analysis is a two-sided t-test with p < 0.001. The recalculation from the posted summary statistics also gives p < 0.001, and the record indicates no discrepancy. Under the stated reporting, the sponsor’s own analysis takes precedence; the recalculation is a supplementary, unadjusted check based on the posted means and standard deviations.

The recalculation reports a mean difference and confidence interval, while the sponsor’s registry entry does not report an estimate or confidence limits. Agreement in the reported p-value does not establish that the methods are identical. The registry record does not say whether the sponsor used a paired t-test, how the crossover structure was handled, or whether adjustments for treatment period, sequence, or carryover were included. It also does not provide participant-level information needed to reproduce a crossover analysis.

Accordingly, the recalculated result is useful for reading the scale and direction of the posted summaries, but it should not be treated as a reconstruction of the sponsor’s full analysis. The sponsor’s test is the reported inferential result, and the recalculation should be understood within its unadjusted assumptions. Neither the agreement in p-values nor the reported direction fills in methodological details that are absent from the registry record.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies a primary endpoint and lists one secondary endpoint. It does not report a multiplicity strategy, such as a hierarchy of tests, an adjustment to significance thresholds, or a plan to control the overall chance of false-positive findings across outcomes. Without that information, the primary test can be discussed as the prespecified main comparison only to the extent that the registry designation reflects the study plan; the record does not provide a full statistical analysis plan to verify that designation or the analysis timing.

In general, multiplicity becomes relevant when researchers examine several outcomes, timepoints, subgroups, or alternative models. If many tests are considered, interpreting each unadjusted p-value as though it were the only test can overstate the strength of evidence. The presence of a listed secondary endpoint does not by itself establish the number of analyses performed, and the registry reports two analyses in the posted results. It does not explain whether these were the complete set of analyses or how selection of reported results was managed.

Missing-data procedures and analysis populations are also not reported in the registry record. The record does not state how many participants had complete measurements for both intervention periods, whether any observations were excluded, or whether an intention-to-treat or per-protocol population was used. It does not describe imputation, sensitivity analyses, or reasons for missing outcomes. These omissions matter in a crossover trial because incomplete periods can affect whether a participant contributes to a paired treatment comparison.

The registry record also does not describe interim analyses or stopping rules. Their absence from the record cannot be taken to mean that none occurred. Likewise, no particular approach to missingness, multiplicity, or analysis population should be inferred from the reported p-values. The posted results remain interpretable as reported summaries, but fuller assessment of confirmatory strength requires the analysis plan and participant-level accounting.

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

The posted results show a lower mean intestinal transit time under laxative tea than under placebo in this randomized crossover trial. The recalculated mean difference is -26.64 hours, and its 95% confidence interval is -35.94 to -17.34 hours. The registry-reported two-sided test has p < 0.001. These statistics describe the observed comparison and the uncertainty represented by the posted calculation; they do not establish that every participant experienced the same change.

The result is specific to the endpoint, intervention periods and population recorded. It does not establish the effect on all symptoms of chronic constipation, quality of life, adverse events, or longer-term outcomes. Although the study aim includes safety, the registry information described for this analysis does not provide a safety result. The trial’s posted efficacy outcome should not be used as a substitute for missing safety information.

The crossover design allows each participant to receive both interventions, but interpretation depends on analysis of the paired data and on consideration of period, sequence and possible carryover effects. The registry record does not report enough analytic detail to determine how these issues were handled. The recalculated comparison is unadjusted and based on summary statistics; it is not proof that a full crossover model would give the same estimate or precision.

The result also does not establish generalizability beyond the trial’s recorded population and conditions. Enrollment was 20, and the registry identifies chronic constipation, but further details about participant characteristics and setting are not reported in the registry record. The record does not provide the original sample-size rationale, missing-data procedures, or the sponsor’s estimate and confidence interval. Those limits counsel against treating a statistically small p-value as a complete account of the evidence.

Overall, the registry reports a clear direction in the posted primary comparison, with an interval that excludes no mean difference under the recalculation. The appropriate conclusion is confined to that result and its stated assumptions. It neither establishes a universal treatment effect nor answers questions that the recorded outcomes and analysis details do not address.

17. Why This Trial Matters Statistically

This trial is statistically interesting because a crossover design changes what a treatment comparison means. Participants can serve as their own reference across intervention periods, which can reduce the influence of stable differences between people. At the same time, valid interpretation depends on preserving the pairing and considering period and sequence effects. Aggregate treatment summaries alone do not expose the within-person relationship that a paired analysis uses.

The posted primary summaries show a marked difference in mean transit time, while the registry’s own test and the unadjusted recalculation report p < 0.001. This contrast makes the distinction between a result’s direction, its magnitude, and its precision important. A p-value indicates evidence under a test’s assumptions; it does not replace an effect estimate, confidence interval, or design-aware analysis.

The record also illustrates why transparent methods matter. The sponsor’s test is reported, but its estimate, interval, crossover model and missing-data handling are not. The recalculation makes the aggregate contrast easier to interpret, yet cannot recover participant-level pairing or establish how the trial’s analysis addressed sequence and period. Statistical transparency is not a technical extra: it allows readers to understand what is being estimated and which assumptions support the inference.

Finally, planning illustrations based on an observed effect should not be confused with the original design rationale or with observed power. They demonstrate how required sample size depends on the effect chosen and target power, but do not explain why this trial enrolled its recorded number. Keeping design planning, observed summaries and confirmatory inference distinct is central to a careful reading of a small crossover trial.

18. Limitations

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

The registry record leaves several trial-specific limitations unresolved. Although the design is crossover, it does not report whether the sponsor’s t-test was paired or whether a model accounted for period, sequence, or carryover. A washout period of 9 days is described, but the record does not report evidence that this period was sufficient to remove carryover. This is an uncertainty in the available reporting, not evidence that carryover occurred.

The masking designation is single, but the record does not identify who was masked. It describes a radiologist unaware of treatment allocation for the marker count, which clarifies masking at that measurement step but not for participants, clinical staff, or outcome assessment more broadly. The registry record does not report blinding assessment or details of placebo matching.

The endpoint description identifies radiopaque markers, abdominal x-rays and a standard formula, but does not report further measurement validation or reliability information. The posted summaries do not provide participant-level paired differences, distributions, outliers, or the number with complete measurements across periods. Missing-data handling, exclusions and analysis population are not reported in the registry record.

Enrollment is recorded as 20, but the registry does not report the original sample-size justification. The planning illustration based on the observed effect is not a substitute for that rationale. The registry also does not report a detailed statistical analysis plan, multiplicity control, interim analysis information, or sponsor confidence limits. These gaps constrain assessment of precision and robustness, particularly for a crossover comparison. They do not erase the posted findings, but they limit the strength of conclusions that can be drawn from aggregate registry results alone.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Laxative Effectiveness of a Phytotherapeutic Tea — NCT00872430.
• Registry record last updated 2009-06-17; status last verified 2009-06.
• Results first posted 2009-03-31.
• 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

NCT00872430 is a completed phase 2 randomized, single-masked, placebo-controlled crossover trial sponsored by Hospital de Clinicas de Porto Alegre. The registry lists chronic constipation as the condition, enrollment of 20, study start in 2002-07 and primary completion in 2002-12. Participants received placebo and Klein Laxative Tea in different sequences, with a washout period of 9 days.

The primary endpoint was intestinal transit time in hours, assessed using radiopaque markers and abdominal x-rays. The posted means were 42.3 hours for placebo and 15.66 hours for tea; the recalculated tea-minus-placebo difference was -26.64 hours, with a 95% confidence interval from -35.94 to -17.34 hours. The registry reports p < 0.001. One secondary endpoint concerning no evacuation after each intervention period is also posted.

The aggregate results indicate a lower mean transit time under tea, but the registry record does not report the full crossover analysis, missing-data methods, analysis populations, or original sample-size rationale. Those omissions limit assessment of the result’s design-specific precision and robustness.