Dose Escalation and Remission (DEAR): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Dose Escalation and Remission (DEAR) (NCT00652145), a randomized phase 4 study. The primary outcome is Fecal Calprotectin Level <50µg/g.

2. Clinical Question

The study summary links FCP to inflammation and relapse risk in quiescent ulcerative colitis. It describes monitoring FCP and using treatment changes for participants with persistently elevated values. The registry record also lists follow-up to week 48 to determine clinical relapse, including for people excluded from the randomized trial because of low FCP at baseline. However, a clinical-relapse result is not reported in the registry record. The available primary comparison therefore addresses the short-term biomarker threshold, rather than whether the treatment strategy changed longer-term relapse.

3. Trial Design

The registry record identifies DEAR as a phase 4, randomized, parallel-group trial with no masking. The listed condition is ulcerative colitis, and the intervention is mesalamine. The record reports enrollment of 119 and status as completed. The posted primary endpoint results contain 26 participants in each arm: one arm increased mesalamine dose by 2.4 g/day, and the other maintained the mesalamine dose described as 2.4 g/day.

The study summary describes a plan to observe 60 patients with FCP below 50µg/g for 48 weeks and to measure FCP at enrollment, 6 weeks, and 12 weeks. It also describes treatment changes for patients with persistently elevated FCP, including a change in formulation to Lialda and/or an increase in Lialda dose. The randomized comparison, as posted, is narrower: increase the mesalamine dose or maintain it. The registry record does not explain how the described observation group relates to the posted randomized arms or to the total enrollment.

The primary outcome is FCP below 50µg/g 6 weeks after randomization. The study summary says the proportion achieving that outcome would be compared using Fisher's exact test. Two additional posted endpoints concern FCP thresholds below 100µg/g and below 200µg/g at 6 weeks. Although the summary describes follow-up for clinical relapse through week 48, a clinical-relapse outcome result is not reported in the registry record. The record also does not report the trial's original sample-size justification or further details of the statistical analysis plan.

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: Among 61 pts with FC \>=50 µg/g at week 0, 26 were taking non-MMX mesalamine at baseline and switched to MMX mesalamine 2.4g/day. Of these, by week 6, 2 had a repeat FC \<50 µg/g, 3 had a flare of UC and 4 were noncompliant with study protocol or no longer interested in participating. The remaining 52 patients were included in the randomized trial.

Overall Study

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 Fecal Calprotectin Level <50µg/g, measured over 6 weeks after randomization.

The primary endpoint counts participants whose FCP level was below 50µg/g 6 weeks after randomization. FCP is a stool marker of intestinal inflammation. The study summary describes it as predictive of relapse risk among people with quiescent ulcerative colitis, which provides the rationale for measuring it as an outcome. The posted endpoint is a threshold response: it records whether each participant was below the specified level at the stated follow-up, rather than the size of any change in FCP from baseline.

In the increased-dose arm, 7 of 26 participants met the threshold; in the maintain-dose arm, 1 of 26 did. These counts describe the registered biomarker outcome. They do not by themselves establish that FCP changed because of treatment, or that a change in this marker corresponded to a change in clinical relapse. The record's summary describes a separate longer-term relapse question, but its result is not reported in the registry record. The endpoint is therefore best read as a short-term comparison of a prespecified FCP threshold, not as a direct measure of symptoms, sustained remission, or relapse.

7. Results Posted in the Registry

• Maintain Mesalmine Dose: 3.8% (1/26) versus 26.9% (7/26) on control; risk difference -23.1 percentage points (95% CI -41.7 to -4.5), risk ratio 0.14 (0.02–1.08); unadjusted two-proportion z-test p = 0.021.

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.

Fecal Calprotectin Level <100 µg/g

• 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:
  • Maintain Baseline Mesalamine Dose: 15.8% (3/19) versus 52.6% (10/19) on control; risk difference -36.8 percentage points (95% CI -64.6 to -9.0), risk ratio 0.30 (0.10–0.92); unadjusted two-proportion z-test p = 0.017.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Maintain Baseline Mesalamine Dose than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Fecal Calprotectin <200 µg/g

• 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:
  • Maintain Baseline Mesalamine Dose: 16.7% (2/12) versus 76.9% (10/13) on control; risk difference -60.3 percentage points (95% CI -91.4 to -29.1), risk ratio 0.22 (0.06–0.79); unadjusted two-proportion z-test p = 0.003.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Maintain Baseline Mesalamine Dose than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry record posts two secondary FCP thresholds, both measured at 6 weeks after randomization: below 100µg/g and below 200µg/g. Across these outcomes, the posted comparisons follow the same general direction as the primary endpoint: the increased-dose arm had more participants below each threshold than the maintain-dose arm. This consistency across thresholds is compatible with the primary biomarker pattern, but it does not make the endpoints independent evidence. They concern related cut points applied to the same type of marker and follow-up period.

The secondary endpoints are not substitutes for the primary threshold, and their results do not answer the longer-term clinical-relapse question described in the study summary. A change in the number of participants meeting a biomarker threshold is not itself a posted result for relapse or another clinical outcome. The registry record does not report a clinical-relapse analysis alongside these secondary results.

The secondary comparisons are posted as unadjusted. When several outcomes are examined, the chance of seeing at least one apparently notable result can increase, even without a true effect. No adjustment for multiple comparisons is reported in the registry record. The secondary p-values should therefore carry less weight than a result from a single prespecified primary endpoint, especially because the endpoints are related and the number of observations differs across them. They can be viewed as context for the primary finding, but should not be presented as separate, definitive confirmations.

Denominators also vary across the posted endpoint results. The registry record does not explain the reasons for those differences or describe how missing measurements were handled. That limits direct comparison of the secondary outcomes with one another and with the primary endpoint. Interpretation should remain tied to each endpoint's recorded population and threshold rather than assuming the same participants contributed to every analysis.

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

• Fecal Calprotectin Level <100 µg/g
• Fecal Calprotectin <200 µg/g

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary: each participant either met the FCP threshold or did not. The arm results are counts of participants meeting the threshold, alongside the numbers in each arm. A risk is the proportion of participants with the outcome in an arm. The posted risk difference compares those risks, and the reported contrast is maintain dose relative to increased dose. A negative risk difference therefore means the recorded outcome was less frequent in the maintain-dose arm. The estimate is −0.231.

What does Fisher's exact test assess?

The study summary says the proportions would be compared using Fisher's exact test. This test evaluates the evidence against equal outcome proportions in the two groups using the observed counts. It is often used for categorical outcomes when the numbers of participants or outcome events are small. The registry record posts an unadjusted p-value of 0.021 for the primary comparison. “Unadjusted” means the reported value is not described as adjusted for multiple comparisons or other covariates. The registry record does not report a fuller analysis plan, such as any prespecified adjustment strategy.

How should a p-value be read?

A p-value is calculated under a null model, here a model in which the groups have equal outcome proportions. It describes how unusual data at least as discrepant as those observed would be under that model and the stated test. It does not quantify the probability that the null model is true, the probability that the result arose “by chance,” or the size of a treatment effect. For interpretation, the p-value should be considered alongside the counts, risk difference, and interval, as well as the endpoint and the trial's limitations.

What do the relative measures add?

The posted risk ratio compares the outcome risks on a ratio scale; the odds ratio compares the outcome odds. For maintain dose relative to increased dose, the risk ratio is 0.143, with interval 0.019 to 1.081, and the odds ratio is 0.109, with interval 0.012 to 0.959. Ratios below 1 indicate a lower observed outcome frequency in the maintain-dose arm relative to the increased-dose arm, but the intervals show uncertainty. The odds ratio is not the same quantity as the risk ratio, particularly for outcomes that are not rare. The risk difference remains useful because it expresses the contrast in absolute risk terms.

Why use an interval as well as an estimate?

An interval gives a range of effect values that are compatible with the data under the method used to calculate it. A narrower interval indicates greater precision; a wider interval indicates less precision. The reported risk-difference interval runs from −0.417 to −0.045. It indicates that the estimated contrast is uncertain even though the full interval lies below zero. The registry record does not specify the interval construction method or confidence level, so those details should not be inferred.

In general, small numbers of participants and outcome events can make estimates sensitive to the outcomes of individual participants. That matters in this comparison, where the posted arm counts are 26 in each group and the primary outcome counts are 7 and 1. The size of the p-value alone does not remove the uncertainty reflected in the interval, nor does it resolve questions about missing data or the population represented by the results.

The secondary endpoints are also binary FCP thresholds. Their posted comparisons have unadjusted p-values, but the registry record does not report a multiple-comparison procedure. Looking across several outcomes creates more opportunities for a nominally small p-value to occur even if there is no effect on any outcome. Accordingly, the secondary findings should be treated as supportive or exploratory rather than as independent confirmation of the primary result.

11. Confidence Intervals and Precision

The primary risk-difference estimate is −0.231, and its reported interval extends from −0.417 to −0.045. The interval gives a sense of the uncertainty around the estimate: values across that range are compatible with the observed data under the interval method. The registry record does not report the interval's confidence level or construction method, so neither should be assumed.

The interval lies entirely below zero, which is consistent with a lower frequency of FCP below 50µg/g in the maintain-dose arm than in the increased-dose arm under the stated contrast direction. Its width also shows that the size of the difference is not precisely determined. The posted arm counts are small, and only 7 and 1 participants, respectively, met the endpoint. With sparse binary outcomes, individual observations can have substantial influence on an estimated contrast.

The relative-effect intervals add another view of uncertainty. The risk-ratio interval is 0.019 to 1.081, and the odds-ratio interval is 0.012 to 0.959. The risk-ratio interval includes 1, while the odds-ratio interval does not. These distinct measures and interval results should be read on their own scales; they do not replace the primary risk-difference estimate or establish a clinical outcome effect.

Precision concerns how narrowly the effect is estimated, not whether a result is important. The registry record does not report outcome completeness, missing-data handling, or a full analysis population definition, which limits assessment of how representative the posted estimate is. The interval quantifies sampling uncertainty under its method, not every source of uncertainty in the conduct or reporting of the trial.

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 displayed planning figures are participants per arm for the binary outcomes, not total events. They are illustrations based on the observed effect, not the trial's original design assumptions. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation; each illustration uses the stated fraction of the observed effect. The original trial's sample-size justification is not reported in the registry record.

For each stated effect size, the 80% power column gives the number of participants per arm estimated to provide an 80% chance of detecting that effect under those planning assumptions if the assumed effect is present. The 90% power column gives the corresponding number for a 90% chance. These are design illustrations, not probabilities that the observed trial result is correct. This is not observed power.

The rows use 100%, 75%, and 50% of the observed effect. The smaller the effect planners want to detect, the more participants are generally needed, because smaller differences are harder to distinguish from random variation. Thus, the entries for planning for 50% of the observed effect are larger than those for planning for the full observed effect. These calculations use the observed effect as a reference and should not be mistaken for the assumptions used to design or conduct the completed trial. A displayed curve, if considered alongside the figures, is a visual aid to this same planning relationship, not an additional trial result.

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

Worked calculation for this trial

1. Control proportion p₀ = 0.269; treatment proportion p₁ = 0.038; average p̄ = 0.154.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5102 = 1.0001.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4835 = 0.4069.
4. n = (1.0001 + 0.4069)² / (-0.2308)² = 37.2, rounded up to 38 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 <- 0.269230769230769                          # control proportion
p1 <- 0.0384615384615385                          # 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(652145)
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 = 38 (80% power), 50 (90% power)
 75% of observed effect: n per arm = 78 (80% power), 103 (90% power)
 50% of observed effect: n per arm = 196 (80% power), 262 (90% power)
power.prop.test: 37.2 
Simulated power at n = 38 per arm: 0.863 (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.

14. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when several statistical questions are tested in the same study. The record reports one primary FCP threshold and two secondary FCP thresholds, all at 6 weeks after randomization. It also describes clinical-relapse follow-up through week 48 in the study summary. Testing several outcomes can raise the chance of obtaining at least one small p-value even when no underlying differences exist. A multiplicity strategy might define which result is confirmatory or adjust the testing procedure, but such a strategy is not reported in the registry record.

The primary comparison has an unadjusted p-value, and the secondary comparisons also have unadjusted p-values. The registry record lists no reported analyses for the secondary endpoints. It does not describe a hierarchy among the endpoints, whether the secondary analyses were planned before results were known, or whether any multiplicity adjustment was used. The secondary results consequently warrant more cautious interpretation than the primary comparison.

Missing-data handling and the analysis populations are also not reported in the registry record. The primary endpoint has 26 participants in each arm, while the record reports overall enrollment of 119. The relationship between total enrollment, the study summary's description of observation, randomization, and the endpoint denominators is not explained. No reason for the different denominators across endpoint results is given. It is therefore not possible to determine from the registry record whether the posted results use all randomized participants, an available-case population, or another analysis set.

The record does not state how missing FCP measurements were handled, whether participants were analyzed according to their randomized assignment, or how protocol deviations were addressed. These details matter because analyses that exclude participants with missing outcomes can differ from analyses that retain all randomized participants under a stated missing-data approach. The record also does not report sensitivity analyses to assess the effect of missing outcomes. These omissions limit assessment of the robustness and generalizability of the posted estimates; they do not establish that particular procedures were or were not used during the trial.

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 0% reporting threshold.

Most frequent non-serious adverse event terms

The posted serious adverse event figures are 0 of 26 participants in the increased-dose arm and 0 of 26 in the maintain-dose arm. These are counts within the recorded groups, not evidence that serious adverse events were impossible or that there was no safety risk. With these group sizes, the figures describe only what was recorded for the participants included in this safety result.

The record also posts 11 of 26 participants with other adverse events in the increased-dose arm and 7 of 26 in the maintain-dose arm. The registry record does not define the “other” adverse-event category in the posted summary or provide event terms for these counts. It lists no serious adverse-event terms. Death counts are not reported in the registry record. The available figures do not provide event severity details, timing, relatedness to treatment, or information about withdrawals due to adverse events. They should be read as a limited summary of recorded counts, not as a complete safety assessment.

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

The posted primary result describes a difference between randomized arms in the proportion of participants meeting an FCP threshold at 6 weeks. The increased-dose arm had 7 of 26 participants below 50µg/g, compared with 1 of 26 in the maintain-dose arm. The estimated risk difference and its interval give a statistical description of that short-term comparison. The result is about a stool biomarker, not a direct measure of clinical relapse or sustained remission.

The study summary explains why FCP was of interest: it is a marker of intestinal inflammation and is described as predictive of relapse risk in quiescent ulcerative colitis. That rationale does not make a biomarker threshold equivalent to a clinical outcome. The registry record describes following participants to week 48 to determine relapse, but a relapse result is not reported in the registry record. No conclusion about that outcome can be drawn from the primary FCP comparison alone.

The comparison also does not establish the effects of every treatment approach mentioned in the summary. The summary describes possible changes in mesalamine formulation and/or dose for people with persistently elevated FCP, while the posted randomized arms compare dose increase with dose maintenance. The record does not report results for a separate formulation comparison.

Statistical evidence should be considered with the size and precision of the estimate, the small posted arm counts, the missing analysis details, and the outcome's meaning. The p-value is not a measure of clinical importance, and the interval does not capture all uncertainties about missing measurements or which participants contributed to the results. The registry record supports a description of the posted short-term biomarker comparison, but not a claim that the strategy changed relapse or other unreported outcomes.

17. Why This Trial Matters Statistically

This trial is statistically instructive because its primary result is a binary biomarker endpoint with small arm counts. The contrast can be expressed as a risk difference, which communicates an absolute difference, or as a risk ratio and odds ratio, which use relative scales. These measures answer related but distinct questions. Reading them alongside the counts and interval helps avoid relying on a p-value alone.

The result also illustrates why precision and statistical evidence are separate considerations. The unadjusted p-value is 0.021, while the risk-difference interval spans a range of plausible effects. A result can be compatible with a difference between groups while still leaving uncertainty about its size. This distinction is important in small studies and when outcome events are sparse.

Another statistical issue is the connection between a surrogate or biomarker outcome and a clinical outcome. FCP is the stated primary endpoint, while clinical relapse is described as a longer-term follow-up question. Those outcomes should not be conflated. The registry record does not report the relapse result, so the primary biomarker comparison cannot answer that separate question.

Finally, the record demonstrates the importance of transparent analysis reporting. The primary test is described, but the record does not report the original sample-size justification, missing-data handling, analysis populations, or multiplicity approach. Those details affect how confidently readers can assess the estimates and secondary findings. Clear reporting of these elements is important for interpreting the strength and limits of a trial result.

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 trial-specific details needed to interpret the posted results are not reported in the registry record. Although enrollment is listed as 119, the primary endpoint groups each contain 26 participants. The record does not reconcile these numbers with the study summary's description of observing 60 patients or explain how participants moved from observation to randomization. It also does not report the numbers screened, randomized overall, or excluded from each endpoint analysis.

The primary outcome denominators differ from those posted for the secondary outcomes, and the record does not explain why. Missing FCP data, the analysis population, adherence, protocol deviations, and sensitivity analyses are not reported. This makes it difficult to assess whether the posted comparisons represent all randomized participants or how robust the estimates are to unavailable outcomes.

The record reports no masking and does not give further details about outcome measurement or allocation procedures. The study summary describes FCP measurement using a commercially available assay, but does not report additional assay procedures or outcome-assessment safeguards. The original sample-size justification and any interim analyses are not reported in the registry record.

The primary result concerns an FCP threshold at 6 weeks. Clinical relapse is described as a follow-up outcome, but its result is not reported. The posted safety summary is also limited: serious-event counts are given, other adverse-event counts are not accompanied by terms, and death counts are not reported. These limitations restrict interpretation to the specific posted endpoints and counts rather than supporting conclusions about longer-term clinical outcomes or comprehensive safety.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Dose Escalation and Remission (DEAR) — NCT00652145.
• Registry record last updated 2015-05-05; status last verified 2015-05.
• Results first posted 2015-05-05.
• 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 record describes the completed DEAR phase 4 trial as randomized, parallel-group, and unmasked, with enrollment of 119. The posted primary endpoint is FCP below 50µg/g 6 weeks after randomization. It records 7 of 26 participants meeting the threshold after a mesalamine dose increase and 1 of 26 after maintaining dose. The risk difference for maintain dose relative to increased dose is −0.231, with an interval from −0.417 to −0.045 and an unadjusted p-value of 0.021.

Two secondary FCP thresholds are also posted. The study summary describes week-48 clinical-relapse follow-up, but the relapse result is not reported in the registry record. Missing-data methods, analysis populations, multiplicity handling, and the original sample-size justification are also not reported. The available findings therefore describe short-term biomarker comparisons, with limited information about participant flow and outcome completeness.