SMS Turkey: Harnessing the Power of Text Messaging to Promote Smoking Cessation: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for SMS Turkey: Harnessing the Power of Text Messaging to Promote Smoking Cessation (NCT00912795), a randomized na study. The primary outcome is Carbon Monoxide-verified Continuous Abstinence at 12 Weeks.

2. Clinical Question

3. Trial Design

This was a randomized, parallel-group trial with no masking. The registry lists the phase as not applicable. A total of 151 participants were enrolled: 76 were assigned to SMS Turkey and 75 to the brochure control. The study was conducted in Turkey, with a start date of 2010-12 and primary completion in 2011-09; its status is completed. The sponsor was the Center for Innovative Public Health Research.

The intervention was behavioral rather than a medication. SMS Turkey delivered daily text messages over 6 weeks, while the comparison group received a 7-page brochure containing general information and tips on quitting smoking. Because masking was listed as none, the trial should be understood as an unmasked comparison. The registry record does not report further details about how randomization was generated or concealed, or whether outcome assessors were masked.

The primary outcome was assessed at 12 weeks after the quit day. The registry also lists three secondary abstinence outcomes: carbon monoxide-verified 7-day point-prevalence abstinence at 4 weeks, self-reported 7-day point-prevalence abstinence at 12 weeks, and self-reported 30-day point-prevalence abstinence at 12 weeks. The trial therefore includes both a continuous-abstinence endpoint and shorter-window point-prevalence endpoints. The registry record does not report the original sample-size justification or the assumptions used to plan the trial.

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: Of the 247 people who expressed interest in participating, 230 were eligible for the study. A total of 151 adults (66% of those eligible) attended the enrollment meeting, where they consented to take part in the research study and were randomly assigned to either the intervention or control group.

Overall Study

Analysis population for the primary outcome, as defined in the registry: Intention-to-treat (ITT) analysis: All participants randomized at baseline included in analyses regardless of completion of 12-week follow-up data. Missing equals failure (i.e., smoked cigarettes).

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 Carbon Monoxide-verified Continuous Abstinence at 12 Weeks, measured over 12-weeks post-quit day.

The primary endpoint counted participants who met the registry’s definition of carbon monoxide-verified continuous abstinence at 12 weeks after the quit day. The definition combined self-report of continuous abstinence since the quit day, allowing no more than 5 cigarettes, with a carbon monoxide reading no higher than 8 ppm. The endpoint is binary at the participant level: a participant either met the stated criteria or did not. The posted result is therefore a count in each randomized group, rather than a measure of the number of cigarettes smoked or the length of time until a participant smoked.

Using both self-report and a carbon monoxide reading makes the outcome more specific than self-report alone, because it requires an additional measurement consistent with the registry’s threshold. The continuous-abstinence definition also asks about smoking over the period since the quit day, while point-prevalence outcomes ask about abstinence over a shorter specified window. These endpoints capture different aspects of quitting and should not be treated as interchangeable.

The primary analysis used an intention-to-treat population: all participants randomized at baseline were included regardless of whether they completed 12-week follow-up. Missing primary-outcome data were classified as failure, meaning the participant was counted as having smoked. The registry record does not report how many participants had missing follow-up data.

7. Results Posted in the Registry

• SMS Turkey: 10.5% (8/76) versus 5.3% (4/75) on control; risk difference 5.2 percentage points (95% CI -3.4 to 13.8), risk ratio 1.97 (0.62–6.28); unadjusted two-proportion z-test p = 0.238.

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.

CO-verified 7-day Point Prevalence Abstinence at 4 Weeks

• 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:
  • SMS Turkey: 11.8% (9/76) versus 9.3% (7/75) on control; risk difference 2.5 percentage points (95% CI -7.3 to 12.3), risk ratio 1.27 (0.50–3.23); unadjusted two-proportion z-test p = 0.617.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between SMS Turkey and the control. The interval gives the range of effects that remain compatible with the data.

Self-reported 7-day Point Prevalence Abstinence at 12 Weeks

• 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:
  • SMS Turkey: 13.2% (10/76) versus 5.3% (4/75) on control; risk difference 7.8 percentage points (95% CI -1.3 to 17.0), risk ratio 2.47 (0.81–7.52); unadjusted two-proportion z-test p = 0.097.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between SMS Turkey and the control. The interval gives the range of effects that remain compatible with the data.

Self-reported 30-day Point Prevalence Abstinence at 12 Weeks

• 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:
  • SMS Turkey: 10.5% (8/76) versus 5.3% (4/75) on control; risk difference 5.2 percentage points (95% CI -3.4 to 13.8), risk ratio 1.97 (0.62–6.28); unadjusted two-proportion z-test p = 0.238.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between SMS Turkey and the control. The interval gives the range of effects that remain compatible with the data.

The three secondary outcomes cover different definitions and time windows: carbon monoxide-verified 7-day point-prevalence abstinence at 4 weeks, self-reported 7-day point-prevalence abstinence at 12 weeks, and self-reported 30-day point-prevalence abstinence at 12 weeks. Across them, the observed counts are numerically higher in the SMS Turkey group than in the brochure group. However, the uncertainty intervals for the re-calculated comparisons include no difference, and the outcomes are based on limited counts. The posted secondary results therefore do not establish a clear group separation.

This broad pattern is directionally consistent with the primary point estimate, which also has more participants meeting the abstinence definition in the SMS Turkey group. Directional consistency across outcomes can be informative, but these endpoints differ in measurement method, abstinence window, and follow-up time. They are related measures, not independent replications of the primary finding. Their shared participants and overlapping outcome concepts mean that the results should not be treated as separate confirmations.

The secondary comparisons are unadjusted in the posted re-calculations. When several outcomes are examined, the chance of at least one apparently unusual result can increase even when there is no underlying difference. Adjusting for multiple comparisons can address that issue, but a multiplicity plan or adjustment is not reported in the registry record. In the absence of a reported plan, secondary findings deserve less weight than a prespecified primary outcome and should be interpreted as supportive or exploratory rather than definitive. The registry lists three secondary outcomes and one primary outcome; it does not report whether other outcomes were considered in the original analysis plan.

The secondary outcomes do not override the primary result. Taken together, they offer context about different abstinence definitions, while the limited sample and uncertainty across comparisons remain central to interpretation.

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

• CO-verified 7-day Point Prevalence Abstinence at 4 Weeks
• Self-reported 7-day Point Prevalence Abstinence at 12 Weeks
• Self-reported 30-day Point Prevalence Abstinence at 12 Weeks

9. Statistical Interpretation

10. Statistical Methods Explained

What kind of outcome was analyzed?

The primary and secondary outcomes are binary participant counts: each is reported as the number of participants meeting an abstinence definition in each group. For this kind of outcome, a group’s count is often compared with the number of participants assessed or included in that group. A relative measure such as a risk ratio compares the groups’ event proportions, while an absolute measure such as a risk difference expresses the separation between those proportions. These measures answer related but distinct questions: relative scale compares proportional levels, and absolute scale describes the difference in event frequency.

The registry’s sponsor-reported primary analysis is a risk ratio. The posted re-calculation also includes a risk ratio and other unadjusted comparisons. A risk ratio of 1 represents equal event proportions; values above or below 1 indicate a higher or lower observed proportion in the intervention group relative to the comparator, respectively. This general interpretation does not mean that a point estimate alone establishes a real group difference. The uncertainty interval and the limited number of observed events also matter.

What does the confidence interval add?

In general, a confidence interval gives a range of values compatible with the observed data under the assumptions of the analysis. A narrow interval indicates greater precision; a wide interval indicates that the data leave more uncertainty about the size and direction of the effect. For the primary sponsor-reported risk ratio, the 95% interval runs from 0.62 to 6.3. It spans the value representing no relative difference, so the result does not rule out that possibility. Its breadth also means that the estimate does not precisely pin down the size of any relative difference.

A confidence interval is not a list of all possible outcomes, and it does not say that each value inside it is equally plausible. Nor does an interval that includes the no-difference value prove that the groups are equivalent. Equivalence requires a prespecified margin and an analysis designed to assess it; such a margin or an equivalence objective is not reported in the registry record.

How should the p-value be read?

The posted primary re-calculation reports an unadjusted p-value of 0.238. In general, a p-value describes how unusual data at least as discrepant as those observed would be under a specified no-difference model and the assumptions of the test. It is not the probability that the no-difference model is true, nor is it a measure of the clinical importance of the observed difference. The registry-reported primary analysis does not include a p-value. The statistical method used for that sponsor analysis is not reported in the registry record, so the posted p-value should be treated as an unadjusted re-calculation rather than attributed to the sponsor.

What does intention-to-treat mean in this trial?

Intention-to-treat analysis retains participants in their randomized groups, regardless of whether they complete follow-up or adhere to the assigned program. Here, the registry says that all participants randomized at baseline were included in the primary analysis, and missing 12-week data were counted as failure, that is, as having smoked cigarettes. This rule preserves the randomized grouping and avoids analyzing only participants with complete follow-up. It also embeds an assumption about missing outcomes: every missing primary outcome is treated as not abstinent. The number of participants with missing data is not reported in the registry record, and the corresponding missing-data approach for the secondary outcomes is not reported.

What is recalculated and what remains unknown?

The posted re-calculations are simple, unadjusted comparisons based on the group counts and denominators. They do not replace the sponsor’s reported analysis. The registry does not specify the method used for the sponsor’s risk-ratio analyses, whether covariates were included, or whether any other adjustment was made. Details of the original statistical analysis plan, including planned tests, handling of multiplicity, and any interim analyses, are not reported in the registry record. Those details should not be inferred from the fact that results are posted for four outcomes.

General statistical terminology can help describe the data, but it cannot fill gaps in the study record. In particular, the registry does not report the trial’s original power calculation or design assumptions. The separate planning illustration uses its own stated assumptions and is not a description of the original design. The interpretation should therefore distinguish the posted outcome counts and sponsor result from statistical details that remain unreported.

11. Confidence Intervals and Precision

Precision is limited for the primary comparison. The sponsor-reported risk ratio is 2.0, but its 95% confidence interval extends from 0.62 to 6.3. Since that interval includes the no-relative-difference value, the result does not exclude equal risks. Since it also includes values on either side of that point and extends broadly, the data are compatible with materially different relative effects. The point estimate is not precise enough to identify the size of the underlying difference.

The underlying counts are 8 participants meeting the endpoint in the SMS Turkey group and 4 in the brochure group. There were 76 and 75 participants randomized to those groups, respectively. With relatively few observed outcomes, each participant’s classification has substantial influence on the group comparison. The wide interval reflects this uncertainty; it should not be interpreted as evidence that the effect is exactly the point estimate.

The re-calculated unadjusted p-value is 0.238, while the sponsor’s reported interval is the registry’s stated inferential result. A p-value and a confidence interval summarize evidence in different ways, and both indicate that the observed comparison is uncertain. The registry record does not report a sponsor p-value or enough statistical-method detail to establish that its interval was produced by the same method as the re-calculation.

Precision is also different from generalizability. Even a precise estimate would apply most directly to the population and conditions studied; uncertainty about how results transfer to other settings is a separate question. The registry record does not report information sufficient to assess that transfer in detail. Overall, the primary estimate is compatible with a range of group differences and should be read cautiously.

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 planning figures are participants per arm, not total participants and not total events. They are planning illustrations based on the observed effect, rather than the trial’s original sample-size justification. The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; each row uses the stated fraction of the observed effect as the effect to detect. The registry record does not report the assumptions used in the trial’s own original design.

For the primary endpoint, planning for 100% of the observed effect gives 424 participants per arm for 80% power and 567 participants per arm for 90% power. Planning for 75% of the observed effect gives 698 participants per arm for 80% power and 934 participants per arm for 90% power. Planning for 50% of the observed effect gives 1,441 participants per arm for 80% power and 1,928 participants per arm for 90% power.

In general, power is the chance that a planned study will detect an effect of the specified size under the planning assumptions, if that effect is present. The 80% and 90% columns describe different target chances of detecting the chosen effect: the higher target generally requires more participants. The rows compare assumed effects: a smaller effect is harder to distinguish from random variation and therefore requires more participants. The illustrations are not observed power; observed power is not a useful substitute for reading the estimate and its uncertainty after a trial is complete.

The figures depend on the assumptions and effect size used, so they should not be read as a recommended design or as a claim about what the original investigators planned. The original design rationale is not reported in the registry record.

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 = 0.053; treatment proportion p₁ = 0.105; average p̄ = 0.079.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.3821 = 0.7490.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.3804 = 0.3201.
4. n = (0.7490 + 0.3201)² / (0.0519)² = 423.8, rounded up to 424 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 <- 0.0533333333333333                          # control proportion
p1 <- 0.105263157894737                          # 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(912795)
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 = 424 (80% power), 567 (90% power)
 75% of observed effect: n per arm = 698 (80% power), 934 (90% power)
 50% of observed effect: n per arm = 1,441 (80% power), 1,928 (90% power)
power.prop.test: 423.8 
Simulated power at n = 424 per arm: 0.811 (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. Analyses Reported by the Sponsor

The sponsor-reported primary analysis gives a risk ratio of 2.0 with a 95% confidence interval from 0.62 to 6.3. The simple unadjusted re-calculation from the posted counts gives a risk ratio of 1.974 and an unadjusted p-value of 0.238. The point estimates are close: the sponsor’s value is consistent with rounding the re-calculated estimate to one decimal place. The registry record does not report a sponsor p-value or the method used to calculate the sponsor’s interval.

The registry marks no discrepancy between the posted result and the simple re-calculation. That does not establish that every analytical detail is identical; the registry record does not report enough method information to make that determination. The sponsor’s confidence interval is broad and includes the value corresponding to equal relative risks, so the sponsor result itself leaves substantial uncertainty about the direction and size of the comparison.

The re-calculation is useful as a transparent comparison based on the posted participant counts, but it is unadjusted and should not be substituted for the sponsor’s own analysis. The two results should be read together with the endpoint definition, the randomized group sizes, and the missing-data rule.

15. Multiplicity, Missing Data and Analysis Populations

Four outcomes are posted: one primary endpoint and three secondary endpoints. Each outcome creates another opportunity to observe a result that appears notable by chance when many comparisons are considered. Statistical methods for addressing this issue can include prespecifying a single primary outcome, adjusting the interpretation or significance threshold across a family of comparisons, or treating secondary analyses as exploratory. The registry identifies a primary outcome, but a multiplicity procedure or a prespecified hierarchy among the secondary outcomes is not reported in the registry record.

The secondary re-calculations are unadjusted. Their p-values should therefore not be interpreted as if each were the only analysis planned. The registry-reported analyses provide risk ratios and confidence intervals, but the statistical method and any multiplicity handling are not reported. The original statistical analysis plan and any interim analyses are not reported in the registry record. It is not possible to determine from the posted record whether the set of analyses represents the full set that was planned or conducted.

For the primary outcome, the registry specifies an intention-to-treat analysis including all randomized participants, with missing 12-week follow-up classified as failure. This is a clear rule, but the number of participants with missing primary outcomes is not reported in the registry record. Without that count, the extent to which the rule affected the group results cannot be assessed. The registry record also does not report sensitivity analyses using alternative assumptions for missing outcomes.

The missing-data rule for the secondary outcomes is not reported in the registry record. Nor are the number of missing measurements at each follow-up, reasons for missingness, or whether the same participants contributed data to each secondary outcome. These gaps limit assessment of how complete the secondary comparisons are. They do not justify assuming that missing outcomes were handled in the same way as for the primary endpoint.

These reporting gaps do not erase the posted counts, but they constrain how fully the analyses can be evaluated. Multiplicity and missing-data details are particularly relevant when interpreting several related abstinence outcomes from a relatively small randomized trial.

16. 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.

The registry lists no serious adverse events among the 76 participants in the SMS Turkey group and none among the 75 participants in the brochure control group. It also lists zero other adverse events in each group. These figures describe the events recorded in the registry, not proof that no adverse events occurred outside the recorded follow-up or reporting process.

The registry record does not report death counts for either group. It also lists no serious adverse-event terms. The record does not provide further detail about adverse-event definitions, collection procedures, or the period over which events were monitored. With those details unavailable, the zero counts should be read narrowly as the registry’s posted figures. They do not establish that either group is free from risk, and they do not support a broad safety comparison.

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

The posted primary result is a comparison of carbon monoxide-verified continuous abstinence at 12 weeks after the quit day. Eight participants in the SMS Turkey group met the endpoint, compared with four in the brochure group. The sponsor-reported risk ratio is 2.0, but its 95% confidence interval, 0.62 to 6.3, includes the no-difference value and is broad. The result therefore does not establish a precise relative difference between groups.

The point estimate favors a higher observed abstinence proportion in the SMS Turkey group, but it is not enough on its own to show that the difference is reliable or that the program caused a particular outcome. The uncertainty interval allows substantially different interpretations, and the unadjusted re-calculation has a p-value of 0.238. Neither the point estimate nor the p-value should be read as a simple yes-or-no judgment about the program.

The trial was randomized, which supports comparing assigned groups, but it was unmasked, and the registry record does not report every detail of trial conduct or analysis. The primary endpoint combines self-report and carbon monoxide verification, while the secondary endpoints use other abstinence definitions. Those outcomes describe distinct aspects of smoking abstinence and should not be collapsed into one claim.

The posted data do not establish what would happen for people outside this study, in other settings, or with different delivery conditions. The registry record also does not report the original sample-size rationale, the analysis plan’s multiplicity approach, or the sponsor’s statistical method. The appropriate conclusion is limited to the observed counts and their uncertainty, not a general claim that the intervention does or does not work.

18. Why This Trial Matters Statistically

This trial illustrates why a randomized comparison should be read through both its effect estimate and its precision. The group counts point in one direction, but the primary confidence interval is wide and includes the no-difference value. Reporting only the point estimate would hide how much uncertainty remains; reporting only whether a p-value crosses a threshold would hide the range of effects compatible with the data.

It also shows why outcome definitions matter. The primary measure requires continuous abstinence by self-report together with a carbon monoxide reading meeting a stated cutoff. The secondary measures use point-prevalence definitions and vary in follow-up timing and whether abstinence is verified. Each answers a somewhat different question, so consistent-looking directions do not make the outcomes interchangeable.

The registry states the primary missing-data rule, which helps readers understand how participants with incomplete follow-up were handled. At the same time, the number missing is not reported, and the registry does not report the approach for missing secondary outcomes. The record also lacks the original design justification and details about multiplicity and statistical methods. These are not technical footnotes: they affect how confidently readers can judge the analysis.

Finally, planning calculations based on an observed effect should not be mistaken for a property of the completed trial or for its original design. They illustrate how sample-size requirements change with the effect assumed and the desired power. Keeping that distinction clear helps separate post-trial uncertainty from prospective planning.

19. Limitations

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

The primary comparison has few participants meeting the abstinence endpoint, and its confidence interval is broad. This limits precision and makes the estimate sensitive to the classification of individual participants. The randomized groups were similar in size, but the total enrollment was 151, so the findings provide limited information about uncommon outcomes or modest differences.

The study was unmasked. The primary outcome includes a carbon monoxide reading as well as self-report, but the registry record does not report whether outcome assessors were masked or provide details of the measurement process. The record also does not report the randomization-generation or allocation-concealment methods, or enough information to evaluate other aspects of trial conduct.

The primary analysis counts missing follow-up as failure, but the number of missing outcomes is not reported. Missing-data handling for the secondary outcomes is also not reported. In addition, the registry record does not report the original sample-size justification, the full statistical analysis plan, a multiplicity procedure, or the method used for the sponsor’s risk-ratio analysis. These omissions make it harder to assess the scope of planned analyses and the sensitivity of results to analytical choices.

There are three secondary outcomes with different time windows and measurement approaches. Their unadjusted results should be interpreted cautiously, especially because no adjustment plan is reported. The registry record describes the target population as adults in Turkey who smoked and wanted to quit; it does not provide enough detail to establish how broadly the findings apply beyond that group or study context.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: SMS Turkey: Harnessing the Power of Text Messaging to Promote Smoking Cessation — NCT00912795.
• Registry record last updated 2016-10-05; status last verified 2016-08.
• Results first posted 2016-10-05.
• 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.

23. Record Summary

NCT00912795 is a completed, randomized, unmasked, parallel-group behavioral trial sponsored by the Center for Innovative Public Health Research. It enrolled 151 adults in Turkey who smoked and wanted to quit: 76 were assigned to daily SMS Turkey messages over 6 weeks, and 75 to a 7-page brochure.

The primary endpoint was carbon monoxide-verified continuous abstinence at 12 weeks after the quit day. Eight participants in the SMS Turkey group and four in the brochure group met the endpoint. The sponsor-reported risk ratio was 2.0, with a 95% confidence interval from 0.62 to 6.3. The interval is broad and includes no relative difference.

Three secondary abstinence outcomes were also posted. The primary analysis counted missing follow-up as failure, while the number of missing outcomes is not reported in the registry record. Details of the original sample-size rationale, multiplicity plan, and sponsor analysis method are also not reported.