Contingency Management for Smoking in Substance Abusers: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Contingency Management for Smoking in Substance Abusers (NCT00807742), a randomized na study. The primary outcome is Number of Participants Smoking Abstinent in Past 7 Days.

2. Clinical Question

The comparison focuses on the contingency of reinforcement rather than simply whether participants received payments or provided breath samples. The NR condition was designed to account for those features, while CM tied reinforcement to smoking reductions and then abstinence. The registry lists substance abuse as the condition and Brown University as the sponsor. It does not report further details about the residential programs, participant characteristics, or eligibility criteria, so the clinical question should be interpreted within the population description that is recorded.

3. Trial Design

The registry describes a randomized, parallel-group trial with no masking. Participants were assigned to Contingency Management (CM) or Noncontingent Reinforcement (NR). Enrollment was 340. The registry lists the study as completed, with a start date of 2008-10 and primary completion in 2014-04. The phase is listed as NA.

Both arms were framed as adjuncts to smoking support involving nicotine replacement and brief advice. In CM, monetary reinforcement depended on smoking reductions during the first 5 days and abstinence during the subsequent 14 days, with expired carbon monoxide levels used to determine those outcomes. NR was intended to control for payment, daily breath sampling, and staff interaction; payment depended on providing a breath sample rather than on smoking status. The registry’s NR description ends before the full payment-matching procedure is complete.

The primary endpoint was the number of participants smoking abstinent in the past 7 days at 1-month follow-up. The record defines abstinence using expired alveolar carbon monoxide < 10 ppm or salivary cotinine < 16 ng/ml. The analysis population is described as intent to treat, with participants lost to follow-up counted as having smoked. The posted arm counts are 172 for CM and 168 for NR.

The registry reports 20 outcome measures and 20 analyses, but no secondary results are posted. Further details about randomization procedures, allocation concealment, the original statistical analysis plan, and the trial’s original sample-size assumptions are not reported in the registry record. The posted planning illustration is a separate calculation based on the observed effect, not documentation of the trial’s original design rationale.

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:

Analysis population for the primary outcome, as defined in the registry: "Intent to Treat" Note: People who were lost were counted as smoked.

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 Smoking Abstinent in Past 7 Days, measured over 1-month follow-up.

The primary endpoint counts participants who met the registry’s definition of smoking abstinence in the past 7 days at 1-month follow-up. Abstinence had to be confirmed by expired alveolar carbon monoxide < 10 ppm or salivary cotinine < 16 ng/ml. The posted arm results are counts: 16 participants in CM and 13 in NR.

A count endpoint makes the outcome concrete: each participant is classified according to whether the specified abstinence criterion was met. In a randomized comparison, those counts can be related to the number assigned to each arm to describe the proportion meeting the endpoint and to estimate a between-arm contrast. The registry’s unadjusted calculation uses the reported counts and arm sizes. The endpoint definition also makes clear that self-report alone was not the stated confirmation method; biochemical measures were used.

A 7-day abstinence measure at a specified follow-up offers a snapshot of recent smoking status. It does not, by itself, describe abstinence throughout the intervention or over a longer period. The registry record does not report the timing of the 7-day assessment within the follow-up visit, the handling of conflicting biochemical tests, or details about repeated testing. Those details would affect how the endpoint is operationalized, but they are not available in the record.

For the primary analysis, the registry says participants lost to follow-up were counted as having smoked. This rule preserves those participants in the stated intent-to-treat approach while classifying missing follow-up as failure to meet the abstinence endpoint. It is a specific missing-outcome assumption, not direct evidence about smoking status among people who were not observed.

7. Results Posted in the Registry

• Noncontingent Reinforcement (NR): 7.7% (13/168) versus 9.3% (16/172) on control; risk difference -1.6 percentage points (95% CI -7.5 to 4.4), risk ratio 0.83 (0.41–1.68); unadjusted two-proportion z-test p = 0.606.

8. Statistical Interpretation

9. Statistical Methods Explained

The statistical results compare a binary endpoint: participants either met the stated smoking-abstinence definition at 1-month follow-up or did not. For this type of outcome, arm-level counts and denominators can be used to estimate risks, meaning the proportions of participants with the event. The posted results give 16 abstinent participants among 172 in CM and 13 among 168 in NR. The recalculated contrast is oriented as NR relative to CM.

What does a risk difference describe?

A risk difference subtracts one arm’s event proportion from the other arm’s event proportion. It is measured on the proportion scale, so zero represents equal event proportions. A negative estimate for NR relative to CM means the observed event proportion was lower in NR. The uncertainty interval around the estimate includes values on both sides of zero, which means the data are compatible with either direction of difference under that interval method. The exact recalculated risk-difference values are not repeated because they are recorded with more than three decimal places.

What does an odds ratio describe?

An odds ratio compares the odds of meeting the endpoint in one arm with the odds in the other. An odds ratio of 1 represents equal odds. Values on either side of 1 represent different directions of association, depending on which arm is placed in the numerator. The sponsor-reported odds ratio is 1.22, with a 95% confidence interval from 0.57 to 2.63. Because that interval includes 1, it does not show a statistically clear difference under the reported analysis. The recalculated odds ratio uses the opposite contrast orientation, so its direction should not be compared with the sponsor’s number without accounting for which arm is in the numerator.

What does the chi-squared test assess?

The registry reports a chi-squared analysis for the odds ratio. In general, a chi-squared test assesses whether the observed distribution across outcome categories differs between groups more than would be expected under a null hypothesis of no association. It does not measure the size or practical importance of a difference. The p-value is .606 in the sponsor’s analysis. A p-value is the probability, under the test’s null model and assumptions, of observing a result at least as incompatible with that model as the one recorded. It is not the probability that the null hypothesis is true, and it does not establish equivalence.

Why are confidence intervals useful?

A confidence interval communicates uncertainty around an estimate, not just whether a p-value crosses a conventional threshold. For the reported odds ratio, the interval spans values below and above 1. For the recalculated risk difference, the interval spans negative and positive values. In both cases, the observed sample does not pin down the direction of a difference precisely. The width of an interval is affected by the amount of information in the data, including the number of events and the group sizes. The posted counts are limited, which is relevant when interpreting the uncertainty.

What does intent to treat mean in this record?

In general, an intent-to-treat analysis retains participants in the groups to which they were assigned, regardless of adherence or treatment received. The registry identifies the primary population as intent to treat and explicitly says that people lost to follow-up were counted as having smoked. That rule places missing follow-up in the non-abstinent category for the primary endpoint. The record does not state whether any participants crossed groups, discontinued intervention, or had other deviations, nor does it report the number lost in each arm. The handling of missing outcomes beyond the stated rule is not reported in the registry record.

What can be concluded from the analysis methods?

The record contains one sponsor-reported chi-squared result for the primary comparison and an unadjusted recalculation based on the posted summary statistics. It does not report whether the sponsor’s analysis adjusted for baseline characteristics, used other covariates, or applied a different variance method. The recalculation is unadjusted and should not be mistaken for a reconstruction of an undocumented full analysis plan. No statistical analysis plan or original sample-size justification is reported in the registry record.

There are 20 outcome measures and 20 analyses listed, but no secondary results are posted. The registry does not say how the family of outcomes was prioritized, whether a primary hypothesis was prespecified in the analysis plan, or whether adjustments for multiple testing were planned. These omissions limit assessment of how the reported result fits within the complete set of analyses. General statistical practice treats multiplicity as relevant when many hypotheses are examined, because repeated testing can increase the chance of at least one apparently unusual result. Whether and how that concern was addressed in this trial is not reported in the registry record.

10. Confidence Intervals and Precision

The central precision issue is the limited number of abstinence events relative to the group sizes. The posted counts are 16 in CM and 13 in NR. With relatively few events, the estimated difference can be sensitive to a small change in the number classified as abstinent. The confidence intervals communicate that uncertainty more directly than the point estimates alone.

The sponsor-reported odds ratio is 1.22, with a 95% confidence interval from 0.57 to 2.63. That interval includes 1, the value representing equal odds, and covers odds ratios favoring either arm under the sponsor’s direction of comparison. The unadjusted risk-difference interval likewise spans negative and positive values. Neither interval identifies a narrow range of plausible effects around a single direction.

Confidence intervals are not guarantees that the true effect lies within a particular realized interval. In general, a 95% confidence procedure is designed so that intervals produced across repeated samples would cover the target value at the stated frequency, under the method’s assumptions. For an individual study, the interval is a measure of statistical uncertainty, not a measure of bias, data quality, or clinical importance.

The registry does not report a prespecified threshold for a meaningful difference, detailed information about missing follow-up, or alternative sensitivity analyses. Those omissions make it difficult to determine whether the uncertainty is acceptable for a particular decision context. The posted result is best read as an imprecise estimate that does not rule out effects in either direction, rather than as proof of no difference.

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 sample-size figures are planning illustrations based on the observed effect, not the trial’s original design assumptions. They give participants per arm for 80% power and participants per arm for 90% power. The calculation uses a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect.

For planning based on 100% of the observed effect, the illustration gives 5,000 participants per arm for 80% power and 6,693 participants per arm for 90% power. Planning for 75% of the observed effect gives 9,074 participants per arm for 80% power and 12,146 participants per arm for 90% power. Planning for 50% of the observed effect gives 20,830 participants per arm for 80% power and 27,885 participants per arm for 90% power. Smaller effects require more participants because a smaller separation between groups is harder to distinguish from sampling variation.

In plain terms, the 80% column gives the planning size associated with an 80% chance of detecting the specified effect if that effect is present and the assumptions hold; the 90% column does the same for a 90% chance. These are prospective planning probabilities, not probabilities that the trial result is true. They are not observed power. The trial’s own original sample-size justification and design assumptions are not reported in the registry record.

The sample-size section also describes a curve, but the registry record does not provide further curve-specific assumptions beyond the stated planning calculation. Read its figures as illustrative sample sizes for future planning under the stated model, rather than as a reconstruction of what the completed trial was designed to detect.

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 = 0.093; treatment proportion p₁ = 0.077; average p̄ = 0.085.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.3948 = 0.7738.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.3947 = 0.3322.
4. n = (0.7738 + 0.3322)² / (-0.0156)² = 4,999.3, rounded up to 5,000 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 <- 0.0930232558139535                          # control proportion
p1 <- 0.0773809523809524                          # 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(807742)
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 = 5,000 (80% power), 6,693 (90% power)
 75% of observed effect: n per arm = 9,074 (80% power), 12,146 (90% power)
 50% of observed effect: n per arm = 20,830 (80% power), 27,885 (90% power)
power.prop.test: 4999.3 
Simulated power at n = 5,000 per arm: 0.798 (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 sponsor-reported analysis gives an odds ratio of 1.22, a 95% confidence interval from 0.57 to 2.63, and p = .606. The recalculation uses the posted arm counts and denominators to form an unadjusted comparison, and reports a risk difference, relative risk, odds ratio, and unadjusted p-value. The recalculated odds ratio is expressed in the opposite direction from the sponsor’s reported odds ratio, so the point estimates should not be read as contradictory simply because one is below 1 and the other is above 1.

The sponsor’s p-value is .606, and the recalculated unadjusted p-value is 0.606. The registry marks no discrepancy between the reported and recalculated analysis. The sponsor’s analysis takes precedence when a discrepancy is flagged; that condition does not apply in this record. The sponsor result is the registry-reported analysis, while the recalculation is a simple unadjusted re-expression of the posted summary counts.

The record does not explain the sponsor’s choice of contrast coding or provide additional model details. It also does not report whether adjustments or other analysis choices were used beyond the listed chi-squared method. The recalculation should therefore be treated as a check based on the posted summary statistics, not as a replacement for an undocumented full statistical analysis.

14. Multiplicity, Missing Data and Analysis Populations

The registry lists 20 outcome measures and 20 analyses, while no secondary results are posted. The primary endpoint is identified, but the record does not describe a full hierarchy of outcomes or hypotheses. It also does not report a multiplicity-adjustment method or explain whether adjustments were planned.

In general, multiplicity arises when several outcomes, time points, subgroup comparisons, or statistical tests are examined. The more tests conducted, the greater the chance that at least one may produce a small p-value by chance alone, if each is judged separately. Approaches such as prespecifying a primary endpoint, controlling a family-wise error rate, or labeling other analyses exploratory can help readers interpret a collection of results. Which approach, if any, was used in this trial is not reported in the registry record. The number of listed analyses alone does not establish how many statistical hypotheses were tested or how they were related.

The primary analysis population is described as intent to treat. The registry specifically states that participants lost to follow-up were counted as having smoked. This is a conservative classification with respect to the abstinence endpoint, but the record does not report the number lost by arm or the timing and reasons for loss. It also does not report sensitivity analyses using other assumptions about missing outcomes. The impact of missing follow-up on the estimated comparison therefore cannot be assessed from the posted information.

Details about protocol deviations, adherence, crossover, and exclusions are not reported in the registry record. Nor is a statistical analysis plan available in the record to establish whether the posted analysis followed prespecified methods. These gaps matter because analysis populations, missing-data handling, and outcome selection can affect both the estimate and its uncertainty. The posted primary result remains interpretable as the comparison under the stated endpoint and missing-outcome rule, but the completeness of the analysis cannot be evaluated from this record alone.

15. 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.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: psychiatric (13.4%), injury (4.2%), infection (3.5%), respiratory (2.9%), gi (1.8%).

The registry lists serious adverse events affecting 42 participants in CM and 34 in NR. Other adverse events are listed for 142 participants in CM and 143 in NR. Deaths are listed as 9 in CM and 2 in NR. These are the posted group figures; the record does not provide further detail about timing, severity definitions, event relatedness, or how events were attributed to treatment.

The serious-event categories listed most often include Psychiatric at 13.4%, Injury at 4.2%, Infection at 3.5%, Respiratory at 2.9%, GI at 1.8%, and Social Circumstance at 1.7%. The record does not specify in this listing whether those percentages apply across both arms or provide arm-specific values for each category. They should not be interpreted as comparative rates between CM and NR.

Event counts alone do not establish that an intervention caused an event, and the registry does not provide enough information to make that attribution. The figures also do not describe exposure time or event timing. They should be read as the adverse-event counts and categories recorded in the registry, not as a complete account of comparative safety.

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

The posted result answers a narrow question: how many participants met the trial’s stated biochemical smoking-abstinence criterion in the past 7 days at 1-month follow-up in each randomized arm? The counts were 16 in CM and 13 in NR. The unadjusted comparison did not show a statistically clear difference, and its interval allows effects in either direction.

This does not establish that the strategies are equivalent. A non-significant result can arise when the underlying difference is small, when the data are imprecise, or when the study has limited information for detecting the effect of interest. The confidence intervals are broad enough to leave uncertainty about direction and magnitude. The registry does not state an equivalence or noninferiority margin, so the analysis cannot be read as an equivalence test.

Nor does the result demonstrate that either strategy is effective compared with no intervention. Both groups received active study conditions, including support involving nicotine replacement and brief advice, and the comparison was contingent versus noncontingent reinforcement. There was no no-treatment arm described in the registry. The posted contrast therefore concerns the added contingency feature within this trial’s conditions, not the overall effect of all smoking support versus no support.

The result also applies to the recorded endpoint and follow-up. It does not establish sustained abstinence, outcomes at other times, or results for every population or treatment setting. The registry identifies people with substance abuse in residential treatment, but further population details are not reported in the registry record. Secondary results are not posted, and the number lost to follow-up is not specified.

The most defensible reading is descriptive: abstinence counts were close, the unadjusted test was not statistically significant, and uncertainty remains substantial. The findings do not justify a claim that the treatments work or do not work. They also do not settle whether smaller or larger differences could matter in another setting or under a different outcome definition.

17. Why This Trial Matters Statistically

This trial is statistically interesting because it separates the contingency of reinforcement from several features that can accompany a payment-based intervention. The NR condition was intended to control for receiving payments, providing daily breath samples, and interacting with research staff. That design makes the comparison conceptually focused on whether tying reinforcement to reductions and abstinence is associated with a different smoking outcome than tying it to sample provision.

It also illustrates why design details and outcome definitions matter. The endpoint was based on biochemical confirmation at 1-month follow-up, with a specified 7-day abstinence window. The missing-outcome rule counted people lost to follow-up as having smoked. Those choices define what the estimated comparison means and constrain how it can be generalized.

The posted result is a useful example of the difference between a point estimate and its precision. The counts favor one arm numerically, but the unadjusted p-value does not provide clear evidence of a difference, and the interval spans both directions. A non-significant result is not the same as evidence that two approaches are identical. Readers need the estimate and interval as well as the test result to understand the remaining uncertainty.

The record also highlights the limits of registry reporting for statistical review. It lists many outcome measures and analyses but posts no secondary results, and it does not report the original design assumptions or detailed analysis plan. A primary estimate can be read, but its place within all planned analyses and the rationale for the trial’s size remain unclear. These distinctions matter when using a single registry result to understand a randomized comparison.

18. Limitations

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

The registry record leaves important design and analysis details unspecified. Randomization is reported, but the method used to generate the sequence and the approach to allocation concealment are not reported in the registry record. Masking is listed as none. The record does not explain how outcome assessors handled knowledge of assignment or whether laboratory testing was conducted without access to group assignment.

The description of the NR payment procedure is incomplete: it states that payment was contingent on providing breath samples and matched to the expected average earned in CM, but the remaining description is cut off. Further details about intervention delivery, adherence, and consistency across residential settings are not reported in the registry record. The record also does not provide participant characteristics that would help assess how closely the enrolled population represents other substance-abuse treatment settings.

The primary endpoint is limited to a 7-day abstinence window at 1-month follow-up. Longer-term outcomes and the timing of the assessment within follow-up are not reported. The record defines biochemical confirmation but does not explain how conflicting or unavailable test results were handled. It says lost participants were counted as having smoked, but does not report how many were lost in each arm or provide sensitivity analyses for missing data.

The registry lists 20 outcomes and 20 analyses but posts no secondary results. It does not report a full analysis plan, multiplicity strategy, or the original sample-size justification. The adverse-event record gives group counts and leading categories but does not provide sufficient detail about event timing, relatedness, or category-specific arm comparisons. These limitations do not erase the posted primary comparison, but they restrict assessment of its broader context and robustness.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Contingency Management for Smoking in Substance Abusers — NCT00807742.
• Registry record last updated 2019-01-23; status last verified 2019-01.
• Results first posted 2019-01-23.
• 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.

22. Record Summary

NCT00807742, titled Contingency Management for Smoking in Substance Abusers, is a completed randomized parallel-group study sponsored by Brown University. The registry lists enrollment of 340, no masking, a start date of 2008-10, and primary completion in 2014-04.

The trial compared Contingency Management with Noncontingent Reinforcement in people with substance abuse in residential treatment. The primary endpoint was the number abstinent from smoking in the past 7 days at 1-month follow-up, confirmed by expired alveolar carbon monoxide or salivary cotinine. The posted counts were 16 in CM and 13 in NR. The sponsor-reported odds ratio was 1.22, with a 95% confidence interval from 0.57 to 2.63 and p = .606.

The result does not show a statistically clear difference in the posted comparison, and the uncertainty interval includes values on either side of the no-difference value. Participants lost to follow-up were counted as having smoked. The registry does not post secondary results or the trial’s original sample-size assumptions.