Efficacy of Open Label Placebo in Children With FGIDs: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy of Open Label Placebo in Children With FGIDs (NCT02389998), a randomized na study. The primary outcome is The Primary Outcome Measure Was Mean Daily Pain.

2. Clinical Question

The question is about symptom scores observed under the two study conditions, not about whether either approach is effective in general. The posted results combine measurements from the placebo periods and from the no-treatment periods. The registry does not provide the treatment sequence details, baseline pain values, or an adjusted estimate of the difference. Those omissions limit how completely the primary comparison can be reconstructed from the record.

3. Trial Design

This was a randomized, open-label crossover study sponsored by Boston Children’s Hospital. The registry lists the study as completed, with 31 participants enrolled and 30 completing the study. No masking was used. The study population comprised children with abdominal pain related to functional gastrointestinal disorders, including the conditions listed in the registry.

Participants received placebo suspension in one treatment period and no assigned treatment in the other. Each period lasted three weeks. The placebo schedule was twice daily, with an optional third dose; hyoscyamine was available as rescue medication in both conditions. The registry describes pain assessment at the ends of the three-week and six-week treatment periods, before crossover to the next treatment arm. Thus, the recorded comparison combines measurements from both treatment periods rather than describing a conventional parallel-group trial in which each participant remains in one arm.

The primary outcome population description states that all 30 completers received placebo or no treatment in a randomized crossover study. It also says all measurements during placebo were combined and all measurements during no treatment were combined, with statistical models adjusted for order of treatment. The treatment sequence, any washout procedures, and the detailed model specification are not reported in the registry record.

The study also listed use of rescue medications and clinical global improvement as secondary outcomes. The registry lists three outcome measures and three analyses overall, but detailed numerical results are not available for every listed secondary outcome. The original statistical plan, sample-size justification, and rules for handling participants who did not complete the study 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.

Before assignment: Cross over study

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: A total of 30 patients completed the study. All of them received placebo or no treatment in a randomized crossover study. All measurements during placebo are combined. All measurements during no treatment are combined. Statistcal models were adjusted for order of treatment

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.

Population: 30 patients were analyzed

6. Primary Endpoint

The registry lists the primary outcome as The Primary Outcome Measure Was Mean Daily Pain, measured over It will be assessed at the end of the 3-week and 6-week treatment periods (at the end of each treatment arm prior to crossover to the next arm of treatment).

The primary endpoint was mean daily pain, measured with a visual analogue scale in millimetres. The scale runs from 0, indicating no pain, to 100 mm, indicating maximum pain; higher scores represent more severe pain. The registry describes the outcome as a change in mean pain score comparing both treatment arms with baseline and specifies assessment at the end of each three-week treatment period.

A continuous pain score retains gradations in reported symptom severity rather than reducing the outcome to a yes-or-no event. Comparing average scores between study conditions can therefore describe the typical level of pain recorded during each condition. In this crossover study, each participant experienced both conditions, and the registry says the primary statistical models accounted for treatment order. Order matters in a crossover design because scores may be associated with which condition came first; how the registry model handled other crossover features is not reported.

The posted arm summaries give mean scores of 39.9 for placebo and 45.14 for no treatment. The registry does not provide baseline means or the numerical changes from baseline, so the amount of change within each condition cannot be reconstructed from those summaries alone. The endpoint is a symptom measure; it does not by itself describe rescue medication use, global improvement, or other aspects of participants’ experience.

7. Results Posted in the Registry

• No Treatment: mean 45.14 versus 39.90 on control; difference 5.24 (95% CI -3.08 to 13.56), standardized effect d = 0.32; z-test p = 0.217.

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.

Use of Rescue Medications

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard errors.
• Result:
  • No Treatment: mean 3.80 versus 2.00 on control; difference 1.80 (95% CI -9.66 to 13.26), standardized effect d = 0.08; z-test p = 0.758.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between No Treatment and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists use of rescue medications and clinical global improvement as secondary outcomes. The posted numerical results are incomplete across these outcomes: rescue-medication data include a sponsor-reported test, while numerical results for clinical global improvement are not reported in the registry record. The available secondary evidence therefore does not give a complete picture across all listed outcomes.

For rescue medication use, the registry reports a Wilcoxon (Mann-Whitney) test with p = .001. The unadjusted recalculation based on posted summary statistics gives a different result, p = 0.758. These values come from different analyses, and the recalculation is not a reproduction of the sponsor’s rank-based test. Because the record flags a discrepancy, the sponsor’s own analysis takes precedence. The conflict is a reason for caution in drawing a broad pattern from secondary results.

Secondary outcomes can complement the primary endpoint by addressing related but distinct aspects of the study. They do not substitute for the primary outcome, and a secondary result does not resolve the missing adjusted estimate for mean daily pain. The record does not report whether testing across outcomes was adjusted for multiplicity. Without such information, an isolated secondary p-value carries less weight as confirmatory evidence because multiple tests can increase the chance of a nominally notable result occurring by chance.

Overall, the registry’s secondary-outcome record is limited: one outcome has a reported sponsor test that differs from a simple recalculation, and the other lacks posted numerical results. Those limitations make the secondary results less conclusive than a coherent, fully reported set of analyses would be. No broader pattern across all secondary endpoints can be established from the record.

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

• Use of Rescue Medications
• Clinical Global Improvement

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous: it is a mean pain score on a visual analogue scale. The registry reports the mean and standard deviation for each condition. The displayed unadjusted recalculation compares those arm summaries and reports a mean difference, confidence interval, and p-value. It is a simple comparison of posted summary statistics, not a reconstruction of every feature of the original crossover analysis.

What does a mean difference describe?

A mean difference expresses the gap between two group averages in the units of the outcome. Here the comparison is expressed as no treatment minus placebo, so a positive difference means the posted average is higher in the no-treatment condition. Since higher scores on this scale represent more severe pain, direction can be described for the raw averages. But the unadjusted difference is not the sponsor’s adjusted estimate, and the registry does not report the adjusted estimate needed to describe the sponsor analysis’s magnitude and direction.

Why does the crossover design matter?

In a crossover study, participants experience more than one condition. Their measurements under the two conditions are therefore related, rather than necessarily independent. A statistical analysis can account for that relationship and for treatment order. The registry says the primary models were adjusted for order of treatment, but it does not report the model specification or enough detail to recreate that analysis. The recalculation based on posted summary statistics should accordingly be read as unadjusted, not as an alternative version of the sponsor’s ANCOVA.

General statistical explanation: accounting for within-participant dependence can affect standard errors and confidence intervals. An analysis that treats related measurements as independent may not represent the design’s dependence structure. Whether the recalculation differs from the sponsor’s analysis for this reason is not reported in the registry record and should not be assumed.

What does ANCOVA mean in this record?

ANCOVA is a model-based method that compares outcomes while accounting for other specified variables. In this trial, the record identifies ANCOVA as the sponsor’s primary comparison method and says statistical models were adjusted for treatment order. It does not identify the full set of model terms, the adjusted outcome contrast, or its confidence interval. The reported p-value is therefore not enough to reproduce or fully describe the adjusted comparison.

How should the p-values be read?

General statistical explanation: a p-value describes how compatible data are with a specified statistical null model, under the assumptions of the test. It is not the probability that a treatment has an effect, nor a measure of effect size or clinical importance. The registry’s primary ANCOVA result is p < 0.03, while the unadjusted recalculation is p = 0.217. They come from different analyses and should not be interpreted as if they were two estimates from one model. The record flags a discrepancy, so the sponsor’s analysis takes precedence.

The rescue-medication outcome also illustrates why analysis methods matter. The registry reports a Wilcoxon (Mann-Whitney) test for that outcome. A nonparametric test compares distributions or ranks rather than directly testing a difference in means under a normal model. The summary-statistic recalculation for this outcome is a mean-based calculation and is not a reproduction of that Wilcoxon analysis. The reported sponsor test and recalculation do not agree, so the same precedence applies.

Why can variation affect interpretation?

General statistical explanation: dispersion describes how spread out measurements are around a typical value. Greater variation makes it harder to estimate a group average precisely when sample sizes are held fixed. In crossover studies, precision also depends on how measurements within the same participant are related. The posted primary standard deviations describe variation within the condition summaries, but the record does not provide the paired differences or their standard deviation. A paired analysis cannot be reconstructed from the two marginal standard deviations alone.

The planning figures are illustrations based on the observed effect and stated planning assumptions, not evidence about what the original trial was designed to detect. The original design assumptions and sample-size justification are not reported in the registry record. The planning exercise uses a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation, with effects set at stated fractions of the observed effect. It gives participants per arm, not observed power.

Finally, interpretation depends on more than the test method. The registry does not report how missing observations were handled, whether all randomized participants were included in the primary analysis, or whether multiplicity was addressed across outcomes. Those details matter for judging the robustness of the reported tests. Their absence does not prove that no such methods were used; it means they are not reported in the registry record.

11. Confidence Intervals and Precision

The unadjusted recalculation for mean daily pain estimates a difference of 5.24, with a 95% confidence interval from -3.076 to 13.56. The interval is based on the posted summary statistics and does not represent the sponsor’s order-adjusted ANCOVA estimate. It includes zero and spans both a difference in one direction and a difference in the other. The interval therefore reflects substantial uncertainty about the unadjusted contrast’s size and direction.

General statistical explanation: a confidence interval gives a range of values reasonably compatible with the data and the method’s assumptions. It is not a guarantee that the true value lies within the particular interval, nor does it directly indicate clinical importance. A narrower interval indicates greater precision under the analysis assumptions; a wider interval indicates less precision.

The registry reports an ANCOVA p-value of p < 0.03 but does not report the adjusted estimate or a confidence interval for it. The unadjusted interval cannot be used to fill that gap: the estimates arise from different methods, and the primary model accounted for treatment order. Consequently, the record does not show how precisely the sponsor’s adjusted effect was estimated.

The study had 30 completers, and the crossover design means participant-level pairing can contribute to precision. However, the paired differences and their variability are not reported. Without those details, the unadjusted summary-statistic interval should be treated as a limited description of the posted arm summaries, not as a full account of the precision available from the study design.

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 sample-size figures are planning illustrations based on the observed effect, not the trial’s original design calculations. The registry does not report the original sample-size justification or design assumptions. These figures are participants per arm, not total events. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; the effect to detect is set at the stated fraction of the observed effect.

The 80% power column describes the number of participants per arm that the planning calculation estimates would be needed for an 80% chance of detecting the assumed effect under those assumptions, if that effect and model were the basis for a future design. The 90% column uses a higher target probability of detection and consequently gives a larger planned sample size for the corresponding effect assumption. These are planning quantities, not guarantees about what a future study will find.

The rows vary the assumed effect: one uses the full observed effect, while the others plan for smaller fractions of it. Smaller effects are harder to distinguish from random variation, so the calculations require more participants per arm to reach the same target power. The curve should be read as illustrating that relationship, not as an observed result from this trial.

This is not observed power. It does not describe the probability that this completed trial detected an effect, and it does not resolve the discrepancy between the sponsor’s analysis and the unadjusted recalculation. Because the calculation is based on an observed effect from a small study, it is especially important to treat the figures as planning illustrations rather than a forecast of future results.

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 = 5.240; pooled standard deviation σ = 16.433.
2. n = 2 × (1.96 + 0.842)² × 16.433² / 5.240² = 154.4, rounded up to 155 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 <- 5.24                      # observed difference in means
sigma <- 16.4330459744991                     # 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(2389998)
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 = 155 (80% power), 207 (90% power)
 75% of observed effect: n per arm = 275 (80% power), 368 (90% power)
 50% of observed effect: n per arm = 618 (80% power), 827 (90% power)
power.t.test: 155.4 
Simulated power at n = 155 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 an ANCOVA superiority analysis for the primary comparison, with p < 0.03. It does not report the adjusted effect estimate, confidence interval, or enough model detail to reproduce that analysis. Separately, a simple unadjusted recalculation from the posted primary arm summaries gives a mean difference of 5.24, a 95% confidence interval from -3.076 to 13.56, and p = 0.217.

These are not interchangeable analyses. The registry says the primary statistical models were adjusted for treatment order, whereas the recalculation is unadjusted and based only on the posted summary statistics. The record flags a discrepancy. In that situation, the sponsor’s own analysis takes precedence; the recalculation should be understood as a limited check on the posted summaries, not as a replacement for the registry’s reported ANCOVA.

The record identifies the sponsor result as a superiority test but does not give an adjusted contrast that would establish its direction or magnitude. A reported p-value alone cannot supply that missing information. The appropriate reading is therefore to note the sponsor’s reported test, distinguish it from the recalculation, and recognize that the registry lacks the adjusted estimate and confidence interval needed for a fuller account of the primary result.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists a primary outcome and secondary outcomes, but an approach to multiplicity is not reported in the registry record. Multiplicity arises when several outcomes or comparisons are tested: considering more tests can increase the chance that at least one result appears statistically notable even when no underlying difference exists. A prespecified hierarchy, adjustment procedure, or other strategy can help clarify how multiple results should be interpreted, but none is described in the posted record.

The registry reports three analyses overall, including the primary ANCOVA and secondary analyses. It does not say whether the tests were prespecified in a statistical analysis plan, whether any adjustment was applied, or how the primary and secondary outcomes were ordered for confirmatory interpretation. Accordingly, the reported p-values should not be treated as though the record establishes a multiplicity-controlled family of tests.

Missing-data methods are also not reported in the registry record. The study enrolled 31 participants and the primary outcome description says 30 completed the study. The record does not explain the status or outcome data of the participant who did not complete, whether measurements were available for all periods, or how any missing observations were handled. It also does not identify the primary analysis population beyond describing the 30 completers and stating that all received placebo or no treatment in the crossover study.

These gaps matter because analysis populations and missing-data assumptions can affect the estimated contrast and its uncertainty. The record does not establish whether the analysis included only completers or another set of participants, nor does it report sensitivity analyses for missing values. It would be inappropriate to infer a particular method or to assume that missing data were inconsequential.

The registry does state that primary statistical models were adjusted for order of treatment. However, the model specification and other crossover-analysis details are not reported. These reporting gaps do not show that the investigators failed to conduct the relevant analyses; they limit what can be verified from the registry record.

16. Safety Results

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

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

The registry reports zero serious adverse events among 30 participants at risk in the placebo condition and zero among 30 at risk in the no-treatment condition. It also reports zero other adverse events in each condition and zero deaths. These are the posted counts for the two treatment conditions.

The figures describe events recorded in this study; they do not establish that no adverse events could occur. A study with a limited number of participants may not characterize uncommon events precisely. The registry does not provide serious adverse event terms because none are listed, and the record does not supply further detail about how events were collected or attributed across the crossover periods.

The same study participants received both conditions, so the condition-level counts should not be read as results from two separate groups of 30 people. The event counts are descriptive and do not by themselves show a causal difference between conditions. No broader safety conclusion can be drawn from these counts alone.

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

The registry records a randomized, open-label crossover comparison of placebo suspension with no treatment in children with functional gastrointestinal disorders. For the primary pain outcome, the posted means are 39.9 during placebo and 45.14 during no treatment. The registry’s sponsor-reported ANCOVA result is p < 0.03, while an unadjusted recalculation from the arm summaries gives a mean difference of 5.24 with a 95% confidence interval from -3.076 to 13.56 and p = 0.217. These results come from different analyses; the sponsor’s reported analysis takes precedence because the record flags a discrepancy.

The registry does not report the adjusted effect estimate or its confidence interval. Thus, the reported sponsor p-value cannot by itself describe the size or precision of the adjusted difference. The unadjusted recalculation is not a substitute for that missing information, especially because the primary model was adjusted for treatment order in a crossover study.

The findings apply to the study conditions and participants represented in the record. They do not establish how results would generalize to other populations, settings, or treatment schedules. The record also does not provide enough detail to assess all aspects of crossover implementation, missing-data handling, or multiplicity. The rescue-medication outcome has a disagreement between the sponsor-reported test and a summary-statistic recalculation, and numerical results for clinical global improvement are not reported in the registry record.

These results should not be used as a stand-alone conclusion about clinical benefit or harm. They describe reported statistical comparisons and their limitations. The absence of an adjusted estimate, incomplete secondary reporting, and analysis discrepancies restrict the conclusions that can be drawn from the registry record.

18. Why This Trial Matters Statistically

This trial illustrates why design and analysis details matter when interpreting clinical results. A crossover study exposes participants to both conditions, making within-participant relationships and treatment order relevant. The registry says the primary models adjusted for treatment order, but it does not provide the adjusted estimate or enough model detail to reproduce the analysis. Marginal means and standard deviations alone do not preserve all of the information needed to evaluate a paired comparison.

The record also demonstrates the difference between a reported analysis and a simple recalculation from summary statistics. The sponsor’s primary ANCOVA result differs from the unadjusted recalculation. A transparent interpretation keeps those analyses separate and gives precedence to the sponsor’s analysis when the record flags a discrepancy, while noting that the effect size and confidence interval for that analysis are unavailable.

Reporting completeness is central to statistical interpretation. The lack of a reported adjusted estimate, incomplete numerical results for secondary outcomes, and absent details on missing data and multiplicity all limit how much can be learned from p-values alone. The planning illustrations offer a separate lesson: sample-size requirements depend strongly on the effect assumed for planning, and calculations based on an observed effect should not be mistaken for the trial’s original design or its observed power.

For biostatisticians and clinical researchers, the record is a practical example of how design, estimands, analysis methods, precision, and reporting jointly shape the meaning of a result. A statistically notable p-value is only one part of that interpretation.

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 registry does not provide the adjusted primary effect estimate or its confidence interval, although it reports an ANCOVA p-value. The unadjusted recalculation is based on arm-level summaries and cannot reproduce the order-adjusted crossover analysis. The record flags a discrepancy, so the sponsor’s analysis takes precedence, but its magnitude and direction cannot be fully assessed from the posted result.

The crossover design is incompletely described. The registry does not report the treatment sequence details, washout procedures, or the full model specification. It says that models were adjusted for order of treatment, but does not report paired differences or the within-participant variability needed to reconstruct the primary comparison from the summaries.

Enrollment was 31 and 30 participants completed the study. The record does not explain the non-completion, describe missing observations by period, or report missing-data methods and analysis populations in detail. The original sample-size justification and protocol-level assumptions are also not reported in the registry record; the displayed planning calculations are illustrations based on the observed effect, not the study’s own design calculations.

Secondary reporting is incomplete. The registry lists clinical global improvement, but numerical results for that outcome are not reported in the registry record. The rescue-medication sponsor test differs from the simple summary-statistic recalculation. The record does not state whether multiplicity was addressed, which limits interpretation of secondary p-values. Finally, the study was open label, and the registry does not report further information about masking of outcome assessment. These are limitations in what can be concluded from the posted record, not proof that unreported procedures were absent.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Efficacy of Open Label Placebo in Children With FGIDs — NCT02389998.
• Registry record last updated 2021-07-23; status last verified 2021-07.
• Results first posted 2021-07-23.
• 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

NCT02389998 is a completed randomized, open-label crossover study sponsored by Boston Children’s Hospital. It enrolled 31 participants, and the registry states that 30 completed the study. The comparison was placebo suspension versus no treatment, with hyoscyamine available as rescue medication in both conditions.

The primary outcome was mean daily pain on a 0-to-100 mm visual analogue scale, with higher scores indicating more severe pain. The registry reports an order-adjusted ANCOVA superiority result of p < 0.03, but no adjusted effect estimate or confidence interval. An unadjusted recalculation from the posted summaries differs; the record flags a discrepancy, so the sponsor’s analysis takes precedence.

Secondary reporting is incomplete, and details on multiplicity, missing-data handling, and the original sample-size justification are not reported in the registry record. The available results should be interpreted with those limitations in mind.