Investigate the Effect of Different Doses of Lesogaberan (AZD3355) as add-on to PPI in GERD Patients With Partial Response to PPI: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Investigate the Effect of Different Doses of Lesogaberan (AZD3355) as add-on to PPI in GERD Patients With Partial Response to PPI (NCT01005251), a randomized phase 2 study. The primary outcome is Number of Participants With a Change in GERD Symptoms Corresponding to at Least Three More Days of Not More Than Mild Symptoms on Average Per Week During Treatment (Approximately 4 Weeks) Than During Baseline (the 7 Days Before Randomisation).

2. Clinical Question

3. Trial Design

The registry identifies this as a phase 2, randomized, double-masked, parallel-group study. It enrolled 661 participants and is listed as completed. The start date is 2009-10 and primary completion is recorded as 2010-07. The sponsor is AstraZeneca.

The study compared four lesogaberan (AZD3355) doses, each added to PPI therapy, with PPI plus placebo. The dose groups were 60 mg bid, 120 mg bid, 180 mg bid, and 240 mg bid. The registry’s arm counts were 134, 125, 136, and 126, respectively; the placebo group count was 140. The primary outcome description places the treatment observation period at 26-30 days, and the title describes it as approximately 4 weeks.

Randomization assigns participants to treatment groups, while double masking is intended to limit the influence of knowledge of assignment on participants’ reports and other trial processes. A parallel-group design means the groups receive their assigned regimens during the study rather than crossing between treatments. These general descriptions explain the design terms; details of the randomization procedure, masking procedures, allocation concealment, and protocol implementation are not reported in the registry record.

The stated study aims included assessing lesogaberan as an add-on to PPI therapy, comparing it with PPI alone, and examining which investigated dose might be optimal. The brief summary also mentions blood drug levels and tolerability. The posted primary outcome results concern symptom change; the registry record does not report results for blood drug levels or a detailed tolerability analysis in the registry record for this analysis.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Overall Study

Reasons for not completing this period:

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

6. Primary Endpoint

The registry lists the primary outcome as Number of Participants With a Change in GERD Symptoms Corresponding to at Least Three More Days of Not More Than Mild Symptoms on Average Per Week During Treatment (Approximately 4 Weeks) Than During Baseline (the 7 Days Before Randomisation), measured over The 7 days before randomisation (baseline) and during 26-30 days of treatment.

The primary endpoint counts participants whose GERD symptoms changed enough to correspond to at least three more days of not more than mild symptoms on average per week during treatment than during baseline. Baseline is defined as the 7 days before randomisation; treatment is described as 26-30 days. Participants recorded symptom intensity twice daily in an electronic Reflux Symptom Questionnaire diary, using six ordered categories: Did not have, Very mild, Mild, Moderate, Moderately severe, and Severe.

This is a binary outcome: for the endpoint, a participant either met the specified response criterion or did not. It is reported as a number of participants, rather than as a continuous change in symptom score. A threshold-based endpoint can make the clinical meaning of a response easier to describe, because it identifies participants who crossed a prespecified symptom-change criterion. It also discards some detail: participants on opposite sides of the threshold may have similar symptom experiences, and the count does not show the size or pattern of every participant’s symptom change.

The registry record does not report the rule used to handle missing diary entries, the precise calculation translating diary ratings into days of symptoms, or whether the endpoint was assessed in a particular analysis population. Those details matter when interpreting a diary-based threshold, and should not be inferred from the endpoint wording alone.

7. Results Posted in the Registry

• AZD3355 60 mg: 20.9% (28/134) versus 17.9% (25/140) on control; risk difference 3.0 percentage points (95% CI -6.3 to 12.4), risk ratio 1.17 (0.72–1.90); unadjusted two-proportion z-test p = 0.524.
• AZD3355 120 mg: 25.6% (32/125) versus 17.9% (25/140) on control; risk difference 7.7 percentage points (95% CI -2.2 to 17.7), risk ratio 1.43 (0.90–2.28); unadjusted two-proportion z-test p = 0.126.
• AZD3355 180 mg: 23.5% (32/136) versus 17.9% (25/140) on control; risk difference 5.7 percentage points (95% CI -3.9 to 15.2), risk ratio 1.32 (0.83–2.10); unadjusted two-proportion z-test p = 0.244.
• AZD3355 240 mg: 26.2% (33/126) versus 17.9% (25/140) on control; risk difference 8.3 percentage points (95% CI -1.6 to 18.3), risk ratio 1.47 (0.93–2.32); unadjusted two-proportion z-test p = 0.100.

8. Statistical Interpretation

9. Statistical Methods Explained

The outcome is binary because each participant either met the specified symptom-response threshold or did not. For a binary outcome, a risk is the proportion of participants with the event in a group. The registry reports event counts and group sizes, and the posted comparisons express differences between each dose group and placebo. The comparison estimates are simple, unadjusted recalculations from the posted summary statistics. The registry record does not report the sponsor’s detailed statistical analysis methods.

What does a risk difference describe?

A risk difference subtracts the event risk in the comparator group from the event risk in the treatment group. A positive estimate means the event was more frequent in the treatment group in the posted data; a negative estimate means it was less frequent. Its scale is an absolute difference in risks, rather than a relative ratio. For example, the 240 mg comparison has a posted risk difference of 0.083. This is a point estimate, not a guarantee of the underlying effect and not a statement about every participant.

The risk difference is useful because it expresses the contrast on the same scale as the outcome’s occurrence. Its meaning depends on the definition of the event and the population being studied. Here, the event is meeting the diary-based symptom-response criterion during the stated treatment period. It should not be generalized to a different symptom definition, time period, or population without evidence.

Why are relative measures also shown?

A risk ratio compares the event risks between groups as a ratio. An odds ratio compares the event odds between groups. Ratios express a relative contrast, while the risk difference expresses an absolute contrast. They answer related but distinct questions, and their numerical values are not interchangeable. The posted risk ratios and odds ratios are recalculations from the same summary counts. Their interpretation depends on the outcome frequency and on the specific scale; an odds ratio is not itself a risk difference.

For each comparison, the registry record includes a point estimate and interval for the risk difference, as well as relative estimates with intervals. The relative intervals include 1 in all four comparisons, the null value for a ratio. This is consistent with the risk-difference intervals including 0, the null value for a difference. Neither form of interval establishes equivalence. Establishing equivalence would require a prespecified margin and an appropriate analysis, which are not reported in the registry record.

What does a confidence interval contribute?

A confidence interval communicates uncertainty around an estimate. In general, an interval calculated by a specified method is designed to cover the true parameter at its stated confidence level over repeated samples when the method’s assumptions hold. It is not a range containing a known fraction of individual participant outcomes, and it does not assign a probability to the true effect after the data have been observed. The 95% intervals for the risk differences are wide enough to include zero and effects on either side of zero.

Interval width depends on factors such as the amount of information in the data, the frequency of the event, and the statistical method. Sparse event counts can produce substantial uncertainty, especially for comparisons between groups. A difference in point estimates should therefore be read together with the interval, not as a precise ranking of doses.

What does a p-value say?

The posted p-values are unadjusted. In general, a p-value measures how incompatible the observed data, or more extreme data, are with a null hypothesis under a statistical model. It is not the probability that the null hypothesis is true, and it is not the probability that the result occurred by chance. A p-value also does not measure the size or clinical importance of an effect. Here, the p-values should be considered alongside the point estimates, confidence intervals, endpoint definition, and absence of a reported multiplicity plan.

When several treatment groups are each compared with a control, multiple testing can increase the chance of at least one apparently unusual result if no correction or other control is used. A prespecified analysis plan may address this issue through a testing hierarchy or another method. Whether such a plan was used is not reported in the registry record, so the unadjusted comparisons should not be treated as a documented confirmatory family of tests.

Why can over-dispersion matter?

Over-dispersion is a general issue for count models: the observed variation can be larger than a simple model assumes. It can make standard errors too small if the model does not allow for that extra variation. The posted primary endpoint, however, is a binary participant-level response count, and the registry record does not describe a count model or report an over-dispersion assessment. It would not be appropriate to claim that over-dispersion affected these results. More broadly, choosing a model should follow the outcome structure and the prespecified statistical plan.

Because no analysis outputs are reported in the registry record beyond the posted outcome counts and comparisons, important details remain unknown. These include the exact confidence-interval and test procedures, any covariate adjustment, the handling of missing observations, and the analysis population. The recalculations therefore support a transparent reading of the summary statistics, but do not recover every element of the trial’s original analysis.

10. Confidence Intervals and Precision

Precision concerns how tightly the data estimate a treatment contrast. The posted risk-difference intervals extend from -0.063 to 0.124 for 60 mg, from -0.022 to 0.177 for 120 mg, from -0.039 to 0.152 for 180 mg, and from -0.016 to 0.183 for 240 mg. All four intervals include 0. Thus, each is compatible with no difference and also with differences in either direction within the interval limits.

The intervals are broad relative to their point estimates. This means the observed event counts do not pin down the size of the contrast precisely. The counts in the groups were 28, 32, 32, and 33 for lesogaberan, compared with 25 for placebo. The endpoint is a thresholded binary outcome, so the analysis uses whether a participant met the criterion rather than all the detail in the symptom diary. This contributes to the specific interpretation of the estimates but should not be assumed to be the sole reason for the uncertainty.

The point estimates differ across doses, but their intervals overlap substantially. These results do not provide precise evidence for a dose ordering, and a ranking based only on the point estimates would understate uncertainty. The registry record does not report a direct dose-to-dose comparison or a dose-response analysis.

In general, a confidence interval describes uncertainty under the method used to calculate it. It is not a prediction interval for individual participants and does not show the full range of possible outcomes. The registry record does not report enough methodological detail to assess every interval assumption. The intervals and p-values should therefore be understood as unadjusted comparisons derived from the posted summaries, not as a complete substitute for a prespecified trial analysis.

11. 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 participants per arm for 80% power and participants per arm for 90% power. They are not total event counts. They are planning illustrations based on the observed effect for each dose-versus-placebo comparison, not the trial’s own design assumptions. The listed 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 the stated fraction of the observed effect.

The 80% power column gives the planned number of participants per arm under those assumptions for an 80% chance of detecting the specified effect if it were the true effect. The 90% power column gives the corresponding planning number for a 90% chance. Higher target power generally requires more participants under the same assumptions. These are prospective design calculations, not results measured in the trial.

Rows describing planning for 100% of the observed effect use the full observed point estimate as the effect to detect. Rows for 75% and 50% of the observed effect use smaller target effects. Smaller effects need more participants to detect under the same assumptions, which is why the planning numbers rise as the target effect is reduced. Because estimates from a trial can be imprecise, planning directly from an observed effect can be optimistic or unstable; the figures are illustrations rather than a recommendation for a future study.

The displayed calculations use each arm’s observed comparison with placebo. They do not account for trial-specific procedures or adjustments that are not reported in the registry record. The trial’s original sample-size justification and original design assumptions are not reported in the registry record. These figures are not observed power.

12. 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, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.179; treatment proportion p₁ = 0.209; average p̄ = 0.194.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5590 = 1.0955.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5585 = 0.4701.
4. n = (1.0955 + 0.4701)² / (0.0304)² = 2,655.2, rounded up to 2,656 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
p0 <- 0.178571428571429                          # control proportion
p1 <- 0.208955223880597                          # treatment proportion
n_per_arm <- function(power, frac = 1) {
  q1 <- p0 + (p1 - p0) * frac               # smaller effect = fraction of the observed difference
  pbar <- (p0 + q1) / 2
  z_b <- qnorm(power)
  ceiling(round((z_a * sqrt(2 * pbar * (1 - pbar)) + z_b * sqrt(p0 * (1 - p0) + q1 * (1 - q1)))^2 / (q1 - p0)^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 (unrounded n per arm)
cat("power.prop.test:", round(power.prop.test(p1 = p0, p2 = p1, power = 0.80)$n, 1), "\n")

# Simulation: how often does the z-test reject at the 80%-power sample size?
set.seed(1005251)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 2,656 (80% power), 3,555 (90% power)
 75% of observed effect: n per arm = 4,651 (80% power), 6,226 (90% power)
 50% of observed effect: n per arm = 10,304 (80% power), 13,794 (90% power)
power.prop.test: 2655.2 
Simulated power at n = 2,656 per arm: 0.807 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-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.

13. Multiplicity, Missing Data and Analysis Populations

The trial has four lesogaberan dose comparisons with placebo. Considering several comparisons raises a multiplicity question: if each is evaluated separately without adjustment, the chance of at least one nominally unusual result across the set can be higher than for a single test. The registry record does not report whether the sponsor used a multiplicity adjustment, testing hierarchy, or other strategy, nor does it report a prespecified decision rule for the family of dose comparisons. The p-values posted for the comparisons are unadjusted and should be read as such.

The record lists one secondary outcome: absolute change from baseline to the treatment period in percent days with at most mild GERD symptoms. Results for that outcome are not reported in the registry record. The primary outcome is posted, but the registry record does not describe an analysis population such as intention-to-treat, modified intention-to-treat, or per-protocol. It also does not state whether participants were analyzed according to randomized assignment or whether exclusions were applied.

Missing diary data can affect a symptom endpoint, particularly when the endpoint depends on reports over baseline and treatment periods. The record does not report how missing entries were handled, whether imputation was used, or how many participants lacked evaluable diary data. The displayed arm counts therefore cannot establish how missing observations were treated or whether the endpoint denominator represents all randomized participants.

These omissions limit assessment of the robustness and confirmatory status of the comparisons. They do not show that an inappropriate method was used; they mean the relevant methods are not reported in the registry record. The posted comparisons are unadjusted recalculations from summary statistics and cannot resolve missing-data or multiplicity questions that require the protocol, statistical analysis plan, or complete analysis report.

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

The results describe how many participants met a specific diary-based symptom-response criterion in each randomized group during an approximately 4-week treatment period. The posted counts were 28 for AZD3355 60 mg, 32 for 120 mg, 32 for 180 mg, and 33 for 240 mg, compared with 25 for placebo. The unadjusted risk-difference estimates are positive, but each confidence interval includes zero and extends to values in both directions.

This does not establish that lesogaberan added to PPI changed the primary outcome compared with PPI plus placebo. It also does not establish that the regimens were equivalent, or that no effect exists. The results are uncertain, and the intervals allow a range of possible contrasts. The unadjusted p-values do not resolve that uncertainty and are not evidence by themselves that an effect is clinically important or unimportant.

The endpoint refers only to the specified change in GERD symptoms, based on the diary ratings and the stated threshold. It does not capture every aspect of GERD, long-term outcomes, or the experience of participants who did not meet the threshold. The treatment observation period was 26-30 days, so the posted results do not describe outcomes beyond that period.

The registry’s brief study summary mentions blood drug levels and tolerability as study aims, but the results available for this analysis do not provide detailed findings for those aims. Adverse event counts are posted, but denominators at risk are not reported. The record lists serious adverse events affecting 0 participants in each of the 60 mg, 120 mg, and 180 mg groups, and 1 in each of the 240 mg and placebo groups. Other adverse events affected 13, 12, 16, 20, and 9 participants, respectively. These counts alone are not a complete safety comparison.

Overall, the posted data support a cautious description of observed symptom responses and uncertain unadjusted comparisons. They do not establish a preferred dose or settle the study’s broader efficacy and tolerability aims.

15. Why This Trial Matters Statistically

This trial offers a useful setting for understanding how a binary symptom-response endpoint and multiple dose comparisons are interpreted. The response threshold gives a straightforward count of participants meeting a specified criterion, but it does not retain the full detail of the underlying diary ratings. That makes the endpoint interpretable in one way while leaving other aspects of symptom change outside the count.

The results also illustrate why point estimates should not be read alone. The risk-difference estimates are all positive, but their intervals include zero and cover a broad range of possible contrasts. The observed ordering of estimates across doses is not enough to establish a dose-response pattern or identify an optimal dose. Precision and the analysis plan matter when several doses are compared with a common control.

Multiplicity is especially relevant in dose-ranging studies: separate unadjusted comparisons may not answer the same question as a prespecified overall or dose-response analysis. The registry record does not report a multiplicity strategy or a direct comparison among doses. That absence makes it important to distinguish descriptive comparisons from a confirmatory conclusion.

The planning illustrations show another statistical lesson: sample-size requirements depend on the effect a future study aims to detect. Smaller target effects require more participants under the stated assumptions. Using an observed estimate as the planning target is only an illustration, particularly when the estimate itself is uncertain.

Finally, the record’s missing details on analysis populations, diary data, and missing-data handling show why transparent methods reporting is essential. Counts and intervals are useful, but they cannot answer questions that depend on undocumented analysis choices.

16. Limitations

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

The primary endpoint relies on participant diary ratings and a threshold for change. The registry record describes twice-daily ratings on a six-graded Likert scale, but does not report the detailed algorithm used to translate those ratings into the response criterion. It also does not report rules for incomplete diaries, missing baseline or treatment data, or the analysis population. Those gaps restrict evaluation of how consistently the endpoint was assessed.

The reported treatment period is 26-30 days, so these results address a relatively short observation period only. Longer-term symptom outcomes are not reported in the registry record. The record lists an additional outcome concerning absolute change in percent days with at most mild GERD symptoms, but its results are not reported in the information available for this analysis.

The posted treatment comparisons are unadjusted. The registry record does not report an adjustment for multiple dose comparisons, covariate adjustment, a direct dose-to-dose test, or a dose-response model. The confidence intervals are also broad, and the outcome counts are modest; estimates should therefore not be treated as precise rankings of the doses.

Safety interpretation is limited as well. The record gives counts of affected participants but does not report the at-risk denominators for those adverse event summaries, and deaths are not reported in the registry record. Serious adverse event terms listed include Non-Cardiac Chest Pain at 0.8% and Metastatic Gastric Cancer at 0.7%. The record does not provide enough detail to attribute those terms to a treatment or compare their rates across groups.

These are limitations of the registry information available, not proof that the trial did not collect or analyze the relevant data. A protocol, statistical analysis plan, and full results report would be needed to assess those aspects.

17. Related Tutorials

18. Related Statistical Calculators

19. Sources

• ClinicalTrials.gov: Investigate the Effect of Different Doses of Lesogaberan (AZD3355) as add-on to PPI in GERD Patients With Partial Response to PPI — NCT01005251.
• Registry record last updated 2011-04-25; status last verified 2011-03.
• Results first posted 2011-04-25.
• 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.

20. Record Summary

NCT01005251 is a completed phase 2, randomized, double-masked, parallel-group study sponsored by AstraZeneca. It enrolled 661 participants with GERD and a partial response to PPI therapy. The study compared four lesogaberan (AZD3355) doses added to PPI with PPI plus placebo.

The primary outcome counted participants meeting a symptom-response threshold based on diary ratings at baseline and during 26-30 days of treatment. The posted counts were 28, 32, 32, and 33 across the dose groups, and 25 in the placebo group. All four unadjusted risk-difference confidence intervals include zero. The registry record does not report the multiplicity plan, analysis population, or handling of missing diary data, limiting interpretation of the comparisons and their precision.