ADAPT: Addressing Depression and Pain Together: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for ADAPT: Addressing Depression and Pain Together (NCT01124188), a randomized phase 4 study. The primary outcome is Proportion Responding Initially by Treatment Arm During 14 Weeks Post Randomization.

2. Clinical Question

The question concerns the added value of the psychotherapy component within a stepped-care approach, because both groups received higher-dose venlafaxine and the control group received supportive management. It is therefore not a comparison of venlafaxine with no medication, or of psychotherapy with no clinical contact. The posted primary result is a count of participants meeting the combined response definition, rather than separate estimates for depression response and pain response.

The registry describes the participants as seniors living with depression and chronic lower back pain, but the precise age threshold, recruitment setting details, and baseline clinical profile are not reported in the registry record. The results should be read in light of that limited description. The comparison addresses the particular treatment strategies and response criteria recorded for this study; it does not by itself establish how those strategies compare in other populations or care settings.

3. Trial Design

ADAPT was a phase 4, randomized, single-masked, parallel-group study. The registry lists University of Pittsburgh as sponsor and records enrollment of 263 participants. The study is marked completed, with a start date of 2010-05 and primary completion in 2016-02. Further details about the process used to generate or conceal the random allocation are not reported in the registry record.

The two arms differed in the behavioral treatment paired with higher-dose venlafaxine. The study intervention arm combined higher-dose venlafaxine with Problem Solving Therapy for Depression and Pain. The active control combined higher-dose venlafaxine with supportive management. Because the medication was included in both arms, the randomized contrast is between these treatment packages, not between medication and psychotherapy as isolated components. The registry identifies the study as single-masked but does not report which groups of people were masked or how masking was maintained.

The primary outcome was the proportion responding initially by treatment arm during 14 weeks post-randomization. The posted counts are 28 responders among 68 participants in the study intervention arm and 28 among 71 in the active control arm. These outcome denominators are not a description of the full enrollment figure; participant flow and the reasons for any difference between enrollment and the posted outcome denominators are not reported in the registry record.

Two secondary outcomes are listed: change in the Roland Morris Disability Questionnaire from the phase 2 baseline to 14 weeks, and change in the Short Physical Performance Battery from the phase 2 baseline to 14 weeks. The registry records 3 outcome measures and 3 analyses overall. Further detail about the timing and conduct of the phase 2 assessments, follow-up beyond the stated windows, or the statistical methods for the secondary outcomes is not reported in the registry record.

4. Participant Flow and Accounting

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

Overall Study

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 Proportion Responding Initially by Treatment Arm During 14 Weeks Post Randomization, measured over 14 weeks.

The primary endpoint is a joint response measure covering depression and pain. A participant had to meet both parts of the definition: two consecutive PHQ-9 scores of 5 or less, and a reduction of at least 30% on the Numeric Rating Scale (NRS) for pain from study entry. The qualifying depression scores therefore had to occur consecutively; a single low score did not meet the stated response rule. The pain component is based on change from entry rather than an absolute pain score.

The PHQ-9 ranges from 0 to 27, with higher scores indicating more severe depression. The registry describes a score of 5 or less as representing absence of depression. The NRS is a self-reported pain scale ranging from 0 to 20, with higher scores indicating more pain. The primary outcome is reported as a count of participants meeting the combined criterion in each arm, over 14 weeks after randomization.

A combined endpoint is used to require improvement on both dimensions named in the study question, rather than treating improvement in depression alone or pain alone as sufficient response. This makes the outcome clinically interpretable as a joint criterion, but it also means the count does not reveal how many participants met only one component. Separate component response counts and additional information about the handling of missing or incomplete repeated assessments are not reported in the registry record.

7. Results Posted in the Registry

• Study Intervention Arm: 41.2% (28/68) versus 39.4% (28/71) on control; risk difference 1.7 percentage points (95% CI -14.6 to 18.1), risk ratio 1.04 (0.70–1.56); unadjusted two-proportion z-test p = 0.834.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is binary at the participant level: each participant either met the joint response definition during the stated period or did not. The registry reports counts of participants with the event in each arm. The event is not depression improvement alone; it requires the specified consecutive PHQ-9 scores together with the specified NRS pain reduction.

What does the risk difference express?

The unadjusted recalculation uses the active control as the reference and compares the observed response proportions. A risk difference is the response proportion in the study intervention arm minus the response proportion in the control arm. A value above zero means the observed proportion is higher in the intervention arm; a value below zero means it is lower. The recalculated risk difference is 0.017. This is an absolute contrast on the proportion scale, not a relative measure. It should be interpreted alongside its confidence interval, which extends from -0.146 to 0.180.

This recalculation is described as unadjusted because it is based on the posted arm-level counts and does not account for covariates. The registry does not report a covariate-adjusted estimate for this endpoint. An unadjusted comparison can be informative as a direct description of the observed arm counts, but it does not establish how any prespecified adjusted analysis was conducted or whether the trial’s primary analysis used the same approach.

What does the p-value say?

The unadjusted p-value is 0.834. In general, a p-value describes how compatible observed data are with a specified null model, under the assumptions of the test. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect. A large p-value does not prove the treatments are equivalent; it indicates that the observed data do not provide strong evidence against the tested null under that calculation. The test specification and any adjustment used in the trial’s own analysis are not reported in the registry record.

Why do confidence intervals matter?

A confidence interval describes uncertainty around an estimate under the assumptions of the method used. In repeated use of a valid interval procedure, the stated confidence level describes the long-run coverage of the procedure, not a probability that this particular interval contains the true value. The risk-difference interval includes zero and extends in both directions. It therefore does not narrowly identify the direction of the arm difference. The interval is more informative than the p-value alone because it displays a range of effect sizes compatible with the data and method.

How should the hazard ratio be read?

The registry reports a hazard ratio of 1.07 and a 95% confidence interval from 0.63 to 1.80. In general, a hazard ratio compares event rates over time between groups, subject to the model and its assumptions. It is not the same as a risk difference or a ratio of the final response proportions. Interpretation depends on what event was modeled, when follow-up began and ended, how censoring was handled, and whether the model assumptions were appropriate. Those details are not reported in the registry record, so the hazard ratio should be reported as posted without inferring a more specific analysis.

In general, time-to-event methods can use information about when an event occurs and can account for different follow-up times, but they require defined event and censoring rules. The registry’s use of a hazard ratio does not by itself establish which participants or time points contributed to that analysis. The reported estimate and interval also do not establish that the proportional-hazards assumption was assessed or satisfied; that information is not reported in the registry record.

Why does endpoint construction matter?

The response definition combines two scales with different properties: a repeated depression score threshold and a relative reduction in a pain score. Requiring both criteria creates a single clinically interpretable event for the posted count, but it hides the pattern of component outcomes. For example, the combined count alone cannot show how many participants met the depression rule without meeting the pain rule. Component-level results and the rules for handling missing scores are not reported in the registry record.

General statistical practice distinguishes the outcome definition from the method used to compare groups. A clear endpoint definition says what counts as an event; an analysis plan specifies how the resulting data are modeled, which participants are included, and how missing observations are treated. The registry supplies the response definition and arm-level counts, but detailed analysis-plan information is not reported in the registry record. That distinction limits how far the recalculation can be treated as a reconstruction of the trial’s own analysis.

Over-dispersion is a concern in some count-data models when variability exceeds what a chosen model expects. It is not directly relevant to the posted primary analysis as described, which reports participants meeting a binary endpoint rather than a count of recurrent events or an over-dispersed count outcome. The registry does not report enough detail to infer that an over-dispersion model was used or was needed. More generally, model choice should match the outcome structure, and uncertainty estimates depend on that choice.

The distinction between an observed estimate and a planning calculation is also important. The observed arm counts describe the enrolled trial outcome as posted. The sample-size figures are hypothetical planning illustrations based on the observed effect and stated assumptions; they do not measure the probability that this completed trial detected an effect. The original protocol’s sample-size rationale and design assumptions are not reported in the registry record.

10. Confidence Intervals and Precision

The recalculated risk difference is 0.017, with a 95% confidence interval from -0.146 to 0.180. The interval crosses zero, so the data are compatible under this method with a small difference in either direction as well as a range of larger differences. Its width indicates that the estimate is not precise enough to confine the plausible risk difference to a narrow range around the point estimate. This is why the point estimate should not be read alone.

In general, a confidence interval combines an estimate with information about its sampling uncertainty, conditional on the analysis method and its assumptions. It does not account automatically for every possible source of uncertainty, such as bias from missing outcome data, departures from the protocol, or limitations in outcome measurement. The registry record does not report the analysis details needed to assess all such sources for this result.

The posted hazard ratio is 1.07, with a 95% confidence interval from 0.63 to 1.80. This interval also spans values on either side of 1, the null value for a ratio measure. Because the hazard-ratio method and event specification are not reported, its precision should be interpreted as uncertainty around the posted time-to-event estimate rather than as a direct translation of the risk-difference interval.

Neither interval establishes equivalence. Equivalence requires a prespecified margin and an analysis designed to determine whether the interval lies within that margin. A margin and an equivalence analysis are not reported in the registry record. The uncertainty visible in these intervals should therefore remain part of any description of the findings.

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, not total events. They use the observed risk-difference effect as a reference and show illustrations for planning to detect 100%, 75%, or 50% of that observed effect. The calculation assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The original trial’s sample-size justification and design assumptions are not reported in the registry record.

The 80% power column gives the estimated participants per arm under those assumptions for a hypothetical study designed to have an 80% chance of detecting the specified effect if that effect were the true one. The 90% power column gives the corresponding planning number for a 90% chance under the same stated assumptions. These are prospective design illustrations, not a retrospective description of the chance that this completed trial found an effect. This is not observed power.

Planning for 100% of the observed effect gives 12,476 participants per arm for 80% power and 16,702 participants per arm for 90% power. Planning for 75% of the observed effect gives 22,142 participants per arm for 80% power and 29,641 participants per arm for 90% power. Planning for 50% of the observed effect gives 49,729 participants per arm for 80% power and 66,573 participants per arm for 90% power.

The pattern reflects a general principle: smaller effects are harder to distinguish from random variation, so detecting them at the same significance level and power generally requires more participants. These figures are illustrations based on the observed effect, not the trial’s original enrollment target or evidence that any particular future study should use those numbers. They also depend on the assumptions; different assumptions or analysis methods could lead to different planning estimates.

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 = 0.394; treatment proportion p₁ = 0.412; average p̄ = 0.403.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6937 = 1.3596.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6936 = 0.5837.
4. n = (1.3596 + 0.5837)² / (0.0174)² = 12,476.0, rounded up to 12,476 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 <- 0.394366197183099                          # control proportion
p1 <- 0.411764705882353                          # 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(1124188)
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 = 12,476 (80% power), 16,702 (90% power)
 75% of observed effect: n per arm = 22,142 (80% power), 29,641 (90% power)
 50% of observed effect: n per arm = 49,729 (80% power), 66,573 (90% power)
power.prop.test: 12476 
Simulated power at n = 12,476 per arm: 0.802 (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. Analyses Reported by the Sponsor

The registry’s sponsor-reported analysis gives a hazard ratio of 1.07 with a 95% confidence interval from 0.63 to 1.80. The unadjusted recalculation from the posted arm counts gives a risk difference of 0.017, with a 95% confidence interval from -0.146 to 0.180 and an unadjusted p-value of 0.834. These are different measures: one is a time-to-event ratio and the other is an absolute difference in the observed proportions. They should not be expected to match numerically or interpreted as the same estimand.

The registry does not report the sponsor analysis method, event definition for the hazard ratio, model covariates, or analysis-population details. Those omissions prevent a detailed reconciliation of the sponsor result with the recalculation. The recalculation is a simple unadjusted analysis of the posted counts and is not a replacement for a fully specified trial analysis. No discrepancy is flagged in the registry record, so there is no reported conflict requiring one result to supersede the other. The sponsor’s result remains the trial’s own posted analysis; the recalculation provides a separate, transparent comparison based on the arm-level counts.

14. Multiplicity, Missing Data and Analysis Populations

The registry lists 3 outcome measures and 3 analyses overall, including the primary response outcome and 2 secondary outcomes. The secondary outcomes are change in the Roland Morris Disability Questionnaire from the phase 2 baseline to 14 weeks and change in the Short Physical Performance Battery from the phase 2 baseline to 14 weeks. The record does not report whether the analyses were prespecified in a protocol or statistical analysis plan, or whether any multiplicity adjustment was used.

Multiplicity arises when several outcomes, time points, subgroup comparisons, or models are examined. In general, testing multiple questions can increase the chance of at least one apparently notable result arising by chance. Methods such as prespecifying a primary endpoint, using a testing hierarchy, or adjusting significance thresholds can address particular multiplicity concerns. Which approach was planned or used in this trial is not reported in the registry record. The listed number of outcomes and analyses alone does not show whether or how multiplicity was handled.

The record does not report the missing-data strategy for the primary endpoint, the definition of the analysis population, or whether participants were analyzed according to randomized assignment. It also does not report how incomplete repeated PHQ-9 or pain assessments affected response classification. These details matter because a joint response endpoint requires information on both depression and pain criteria, and the depression rule requires consecutive scores. Without the missing-data rules and participant-flow information, it is not possible to determine how incomplete measurements contributed to the posted counts.

The registry reports enrollment of 263, while the primary outcome counts are based on 68 participants in the study intervention arm and 71 in the active control arm. The record does not explain the relation between total enrollment and these endpoint denominators, including whether the difference reflects randomization, eligibility for this phase, available outcome data, or another reason. Those possibilities should not be assumed. The handling of protocol deviations, withdrawals, and participants with no usable endpoint data is also not reported in the registry record.

Further information about prespecified interim analyses, stopping rules, subgroup analyses, and any adjustment for repeated testing is not reported in the registry record. Their absence from the record does not establish that such procedures did or did not occur. It means that claims about them cannot be made from the posted information.

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.

For serious adverse events, the registry lists 0 affected participants among 68 at risk in the study intervention arm and 0 affected participants among 68 at risk in the active control arm. For other adverse events, it lists 0 affected participants among 68 at risk in the study intervention arm and 0 among 71 at risk in the active control arm. These are the posted counts and denominators; the serious-event denominator in the active control differs from the other-adverse-event denominator, and the registry record does not explain that difference.

These figures describe events recorded in the registry for the stated at-risk groups. They do not establish that no events occurred outside the registry’s definitions, collection period, or reporting rules. The record does not provide details about event definitions, severity grading beyond the serious/non-serious distinction, exposure duration, or methods of collecting events. The top serious-event terms list is empty, so no specific serious-event terms are posted there. Death counts are not reported in the registry record.

Zero recorded affected participants should be read as a reported count, not as proof that an intervention has no safety risks. The available safety figures alone do not support a complete comparison of harms, especially without fuller event definitions and follow-up information.

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

The posted primary result shows 28 participants meeting the joint response definition in each arm. The unadjusted recalculated risk difference is 0.017, and its 95% confidence interval ranges from -0.146 to 0.180. The unadjusted p-value is 0.834. Taken together, these statistics do not provide strong evidence of a difference on the unadjusted risk-difference analysis, while the interval remains broad enough to include differences in either direction.

This is not evidence that the two treatment strategies are equivalent. Equivalence requires a prespecified clinical margin and an analysis designed for that question, neither of which is reported in the registry record. The finding also does not establish that one strategy is ineffective. A lack of strong statistical evidence for a difference is not the same as proof that no difference exists.

The comparison is specific to two active packages: higher-dose venlafaxine plus PST-DP versus higher-dose venlafaxine plus supportive management. It does not separate the effect of the medication from the effect of behavioral care, because both arms received the medication. Nor does it compare either package with no treatment. The result applies to the defined joint endpoint during 14 weeks after randomization; it does not directly answer questions about longer-term outcomes or other measures of health and functioning.

The registry also posts a hazard ratio of 1.07 with a 95% confidence interval from 0.63 to 1.80. The analysis details are not reported, so that estimate should not be used to infer more than the posted time-to-event comparison. Similarly, the primary counts do not show how many participants met the depression criterion alone or the pain criterion alone.

Finally, the outcome denominators and missing-data procedures are not fully explained in the registry record. The posted results should therefore be interpreted as the reported analysis, with uncertainty about analysis populations and incomplete outcome data. They do not determine the appropriate treatment for any individual.

17. Why This Trial Matters Statistically

This trial illustrates why a clinical question needs to be matched carefully to the randomized contrast. Both arms included higher-dose venlafaxine, while the behavioral component differed between PST-DP and supportive management. The estimate therefore concerns those two packages in the study setting. Describing it as a comparison of medication against psychotherapy would misstate the design.

It also demonstrates how endpoint construction shapes interpretation. The primary response rule required both a depression threshold sustained across consecutive assessments and a pain reduction criterion. That joint definition reflects the trial’s combined clinical focus, but the posted total response count cannot reveal whether one component drove the pattern or how often participants improved in only one domain. Component-level results would be needed to answer those questions.

The distinction between effect size and statistical evidence is equally important. The risk-difference estimate is 0.017, but its 95% confidence interval extends from -0.146 to 0.180. A point estimate near zero should not be mistaken for a precise estimate of no difference. The interval communicates uncertainty about both direction and magnitude, while the unadjusted p-value alone cannot describe that range.

The registry’s hazard ratio adds a different type of estimate, but without its event definition and model details it cannot be directly reconciled with the risk difference. This is a practical reminder that statistical measures are meaningful only in relation to the outcome, time structure, and analysis method they represent.

Finally, a planning illustration based on an observed effect is not a report of the original trial’s design rationale. Keeping those concepts separate prevents retrospective power claims and makes clear what the registry does and does not establish.

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 does not report detailed eligibility criteria, participant characteristics, or the specific age threshold used for the description of older adults. As a result, the extent to which the enrolled participants represent other groups of people with depression and back pain cannot be assessed from the record alone. Setting details and recruitment procedures are also not reported.

Although the trial is recorded as single-masked, the identity of the masked parties and the procedures used to maintain masking are not reported. Allocation concealment, treatment adherence, fidelity to the psychotherapy approach, and the amount or content of supportive management are also not described in the registry record. These details would help assess how the treatment contrast was implemented.

The primary counts use 68 participants in the study intervention arm and 71 in the active control arm, while total enrollment is 263. The record does not explain the relation between enrollment and these endpoint denominators or provide a participant-flow account. The analysis population, missing-data approach, treatment of incomplete repeated scores, and handling of withdrawals are not reported. These gaps limit assessment of the robustness of the endpoint comparison.

The sponsor-reported hazard ratio has no accompanying method description, event definition, or detailed analysis population in the registry record. The primary unadjusted recalculation is consequently not a full reconstruction of the trial’s own analysis. The record also does not report the trial’s original sample-size assumptions, a prespecified clinically important difference, multiplicity procedures, or interim-analysis procedures.

Safety information is limited to the posted affected-participant counts and at-risk denominators. Event definitions, collection procedures, exposure duration, and death counts are not reported in the registry record. Together, these limitations mean the posted summary supports a bounded interpretation of the recorded outcomes, rather than a comprehensive assessment of the trial’s conduct, efficacy, or safety.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: ADAPT: Addressing Depression and Pain Together — NCT01124188.
• Registry record last updated 2017-05-12; status last verified 2017-04.
• Results first posted 2017-05-12.
• 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

ADAPT is a completed, randomized, single-masked, parallel-group phase 4 study sponsored by University of Pittsburgh, with enrollment of 263. The registry records a start date of 2010-05 and primary completion in 2016-02. The study concerns older adults with depression and chronic lower back pain in a stepped-care setting.

The primary outcome is response during 14 weeks after randomization, defined by two consecutive PHQ-9 scores of 5 or less and an NRS pain reduction of at least 30% from study entry. The posted counts are 28 of 68 in the study intervention arm and 28 of 71 in the active control arm. The unadjusted recalculated risk difference is 0.017, with a 95% confidence interval from -0.146 to 0.180 and an unadjusted p-value of 0.834. The registry also reports a hazard ratio of 1.07 with a 95% confidence interval from 0.63 to 1.80.

Detailed information about analysis populations, missing data, and the sponsor’s hazard-ratio method is not reported in the registry record. Two secondary outcomes concern disability and physical performance.