Evaluation of a Diabetes-specific Cognitive Behavioural Treatment for Subthreshold Depression: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Evaluation of a Diabetes-specific Cognitive Behavioural Treatment for Subthreshold Depression (NCT01009138), a randomized na study. The primary outcome is Depressive Symptoms (CES-D Score).

2. Clinical Question

The trial addressed a practical research question: whether a diabetes-focused group intervention was associated with a different change in depressive symptoms than diabetes education. The primary endpoint was the difference between the baseline and 12-month CES-D scores. The posted group means therefore describe change over time within each group, while the between-group mean difference compares those changes.

The registry’s description frames the project as developing and evaluating an intervention for diabetic patients with subthreshold depression. Its summary also identifies glycaemic control, quality of life, diabetes self-management, health-care costs and inflammatory parameters as areas of interest. The posted secondary outcomes include several of these domains, but the primary statistical comparison concerns depressive symptoms. The record does not report a separate eligibility definition for subthreshold depression or further details about how participants were recruited.

3. Trial Design

The registry identifies this as a randomized, parallel-group trial with no masking. Participants were assigned to Diabetes-Specific CBT (DS-CBT) or Standard Diabetes Education. The listed interventions are both behavioral. The DS-CBT group intervention focused on diabetes-specific problems; the comparator consisted of standard diabetes education lessons, with group contact and knowledge acquisition described as relevant nonspecific effects.

The registry reports enrollment of 214. Its brief summary describes an intended recruitment of 188 diabetic patients, so the summary’s stated intended recruitment and the registry’s enrollment figure are different entries. The record does not explain the reason for that difference. It reports a study start of 2009-11, primary completion of 2012-03, and status as completed. Phase is recorded as NA.

The primary outcome was depressive symptoms measured using the CES-D, with baseline and 12-month follow-up specified. The posted results report mean changes and standard deviations for each group. The primary comparison is a mean difference between the groups’ changes, DS-CBT minus standard education as represented by the posted comparison. The record lists 93 participants for the DS-CBT outcome and 88 for the standard-education outcome. These outcome counts are not a statement about how many participants completed every study activity.

The registry record does not report the trial’s original sample-size justification, the allocation procedure beyond randomization, details of concealment, or a fuller statistical analysis plan. Although the record lists secondary measures, it reports zero analyses in its analysis count and gives no reported analyses for the listed secondary outcomes. The numerical comparisons discussed in the statistical interpretation are simple unadjusted recalculations from posted summary statistics, not a substitute for an unreported sponsor analysis.

4. Participant Flow and Accounting

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

Overall Study

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 Depressive Symptoms (CES-D Score), measured over Baseline, 12 month FU.

The primary endpoint is change in depressive symptoms from baseline to 12-month follow-up, measured with the Center for Epidemiologic Studies Depression Scale (CES-D). The registry describes the instrument as assessing the frequency of 20 typical depressive symptoms during the previous week. Items use a 4-point Likert scale, and the summed score ranges from 0 to 60, with higher scores indicating more severe depressive mood.

The endpoint is a continuous score, and the registry reports the mean and standard deviation of the change in each group. The group means are negative: the registry’s outcome description defines the reported measure as the follow-up score minus the baseline score, so a negative change represents a lower score at follow-up than at baseline. The treatment comparison asks whether the average change differed between randomized groups, rather than whether either group changed in isolation.

Using the same symptom measure at the two specified assessments provides a way to describe change in the outcome that motivated the intervention. The between-group contrast is important because change within one group alone cannot distinguish changes associated with the intervention from changes that may also occur under the education comparator. The registry record does not report an additional clinical threshold for interpreting a difference in CES-D points, so the numerical result should be read as a score difference, not as a classification of individual participants.

7. Results Posted in the Registry

• Diabetes-Specific CBT (DS-CBT): mean -7.40 versus -2.70 on control; difference -4.70 (95% CI -8.07 to -1.33), standardized effect d = -0.41; z-test p = 0.006.

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.

Quality of Life (EQ-5D TTO Score)

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Diabetes-Specific CBT (DS-CBT): mean -0.01 versus -0.01 on control; difference 0.00 (95% CI -0.07 to 0.07), standardized effect d = 0.00; z-test p = 1.000.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Diabetes-Specific CBT (DS-CBT) and the control. The interval gives the range of effects that remain compatible with the data.

Diabetes-specific Distress (PAID Score)

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Diabetes-Specific CBT (DS-CBT): mean -13.00 versus -4.20 on control; difference -8.80 (95% CI -14.02 to -3.58), standardized effect d = -0.49; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Diabetes-Specific CBT (DS-CBT) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Diabetes Self-Care (SDSCA Score)

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Diabetes-Specific CBT (DS-CBT): mean -0.10 versus 0.00 on control; difference -0.10 (95% CI -0.41 to 0.21), standardized effect d = -0.10; z-test p = 0.522.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Diabetes-Specific CBT (DS-CBT) and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes span quality of life, diabetes-specific distress, self-care, acceptance, glycaemic control and inflammatory markers. The posted data therefore cover a broader set of outcomes than the primary depression measure. Across the available numerical secondary comparisons, the pattern is mixed: the outcomes do not all show the same degree or direction of separation between groups. This broader pattern provides context for the primary result but does not make the different measures equivalent.

Secondary measures can help assess whether a primary-outcome pattern is accompanied by changes in other relevant domains. They may also describe areas where group changes appear similar or where the posted estimate is uncertain. They should not be treated as independent replications of the CES-D result, since they measure different constructs and may be related to one another. A difference in depressive symptoms does not, by itself, imply a corresponding difference in quality of life, self-management, glycaemic control or inflammatory markers.

The record lists 12 outcome measures and 11 posted secondary outcomes, but it reports no formal analyses for the secondary outcomes. No multiplicity adjustment or prespecified testing hierarchy is reported in the registry record. In general, evaluating many outcomes without accounting for multiple comparisons can make isolated small p-values less persuasive, because the opportunity for chance findings increases as the number of tests grows. This does not mean a particular secondary result is false; it means that its evidential weight is limited without a reported analysis plan and appropriate context.

For these reasons, secondary results are best read as exploratory descriptions of the posted group summaries rather than as a definitive set of confirmatory conclusions. The primary endpoint remains the outcome identified as primary in the registry. A coherent pattern across outcomes could add context, but the record does not report enough about endpoint prioritization or analysis procedures to establish that such a pattern was tested as a formal hypothesis.

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

• Quality of Life (EQ-5D TTO Score)
• Diabetes-specific Distress (PAID Score)
• Diabetes Self-Care (SDSCA Score)
• Diabetes Acceptance (AADQ Score)
• Glycemic Control (HbA1c)
• Inflammatory Marker IL-6
• Inflammatory Marker IL-1Ra
• Inflammatory Marker Hs-CRP

9. Statistical Interpretation

10. Statistical Methods Explained

The main posted outcome is continuous: each participant’s CES-D result is a score, and the group summaries describe average changes and their variability. A mean is a convenient summary of the group’s average score change. The standard deviation describes how spread out individual changes are around that group average. These summaries do not show the full distribution, so they cannot establish whether changes were similar for all participants or concentrated among some participants.

What does the mean difference represent?

The primary comparison subtracts the standard-education group’s mean change from the DS-CBT group’s mean change. The reported estimate is -4.7 points. Since the outcome is defined as follow-up minus baseline, negative values represent decreases in the score. A negative contrast therefore means the DS-CBT group’s average change was more negative than the comparator group’s average change in the posted summaries. This is a comparison of group averages, not a statement that every participant’s score decreased.

What does the unadjusted calculation include?

The recalculated comparison uses the posted sample sizes, group means and standard deviations. It is an unadjusted summary-statistic comparison. It does not incorporate any covariates, a model for repeated observations, or other adjustments not listed in the record. The record does not report the sponsor’s formal analysis method. A recalculation is useful for describing the numerical contrast and its uncertainty, but should not be presented as if it were the trial’s prespecified analysis.

The reported p-value for the primary contrast is 0.006. In general, a p-value assesses how compatible the observed data are with a specified null hypothesis, under the test assumptions. It does not measure the size or importance of the difference, and it does not quantify the probability that a treatment effect is real. The confidence interval adds information about the range of effect sizes compatible with the data and method. Neither statistic addresses biases or missing information that are not represented in the calculation.

Why does variability matter?

The standard deviations for the primary endpoint are 11.4 in the DS-CBT group and 11.7 in the Standard Diabetes Education group. In general, more variation among individual outcomes makes a group mean less precise when other features are held fixed. A pooled standard deviation is used in the posted standardized effect-size calculation; it is 11.55 for the primary comparison, and the listed standardized difference is -0.407. A standardized effect expresses the mean contrast relative to outcome variability. It can aid comparison across scales, but it does not replace the original score difference or provide a clinical interpretation on its own.

The registry lists the primary outcome at baseline and 12-month follow-up, but does not describe whether the analysis used individual change scores, a repeated-measures model, or another approach. The posted group summaries describe changes, and the recalculation compares those summaries. The distinction matters because different models can use the data and assumptions differently, especially when some follow-up measurements are unavailable. The handling of missing measurements is not reported in the registry record.

Why can over-dispersion matter in other settings?

General statistical context: when outcome variation is greater than a model assumes, standard errors can be too small and uncertainty can be understated. That concern is especially relevant to count outcomes or clustered data when the model’s variance assumptions do not fit. The primary endpoint is reported as a continuous score with group standard deviations; the registry does not report a model that would allow assessment of a specific over-dispersion issue. This general principle should not be mistaken for evidence that over-dispersion occurred in this trial.

Randomization supports a group comparison by assigning participants to intervention conditions, but it does not guarantee that every possible source of bias has been eliminated in the reported outcome analysis. Masking is listed as none. The registry does not report allocation concealment, outcome-assessor masking, or details about adherence. Consequently, the numerical group contrast is best understood alongside the information available about design and analysis, not as a complete account of causal certainty.

How should secondary comparisons be interpreted?

The listed secondary outcomes include quality of life, diabetes-specific distress, diabetes self-care, diabetes acceptance, glycaemic control and inflammatory markers. The registry lists 12 outcome measures and 11 posted secondary outcomes, but does not report formal secondary analyses. The numerical secondary comparisons are therefore descriptive recalculations based on the posted summaries. They are not adjusted for multiplicity in the record. When many outcomes are considered, the chance of at least one apparently notable result can increase; adjustment or a prespecified hierarchy can help manage this issue. The registry record does not report whether such procedures were planned or used.

Interpretation should also separate statistical evidence from clinical importance. The primary interval does not include zero, but the record supplies no minimum important CES-D difference or other threshold for clinical relevance. Nor does a statistically distinct group average reveal how individual outcomes varied. These are general limits of summary-statistic comparisons, not additional findings about participants in this trial.

11. Confidence Intervals and Precision

The primary mean difference is -4.7 CES-D points, with a 95% confidence interval from -8.068 to -1.332. The interval describes uncertainty around the estimated group contrast under the simple unadjusted method used for the recalculation. In general, a confidence interval is a range generated by a statistical procedure that, across repeated samples under its assumptions, would contain the underlying quantity at its stated confidence level at the corresponding rate. It is not a range containing a specified proportion of individual participants’ changes.

Both limits of the primary interval are negative. In the direction used for the comparison, the interval is compatible with a greater average score decrease in the DS-CBT group than in the standard-education group. The interval also conveys that the exact size of the contrast is not known: values across the interval remain compatible with the data and method. The p-value of 0.006 is related to the interval’s test of a zero difference, but it does not make the estimate more precise or resolve the clinical meaning of the score difference.

Precision depends in part on the amount of information and on outcome variability. The reported primary standard deviations are 11.4 and 11.7, and the outcome counts used in the comparison are 93 and 88. These summaries help characterize the calculation, but the record does not provide individual-level data or details of missing outcomes. The confidence interval therefore cannot account for uncertainty from unreported analysis choices or data limitations.

For the EQ-5D comparison, the interval is -0.070 to 0.070; for PAID, it is -14.02 to -3.582; and for diabetes self-care, it is -0.406 to 0.206. The differing scales mean interval widths should not be compared as if they were directly commensurable. These secondary intervals are unadjusted, and their interpretation should account for the number of outcomes considered and the absence of reported multiplicity procedures.

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 sample-size illustrations are planning calculations based on the observed effect, not the trial’s original design assumptions. For these continuous outcomes, the figures are participants per arm. The listed planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; the effect to detect is the stated fraction of the observed effect. The trial’s own original sample-size assumptions are not reported in the registry record.

For the primary outcome, planning for 100% of the observed effect gives 95 participants per arm for 80% power and 127 participants per arm for 90% power. Planning for 75% of the observed effect gives 169 participants per arm for 80% power and 226 participants per arm for 90% power. Planning for 50% of the observed effect gives 379 participants per arm for 80% power and 508 participants per arm for 90% power. The figures apply to the stated assumptions and observed effect used in this illustration.

In plain language, 80% power describes a design that would have an 80% chance of detecting an effect of the specified size at the specified significance level if that effect were the true one and the assumptions held. The 90% power column describes the corresponding design with a higher chance of detecting that specified effect. Smaller target effects need more participants to distinguish them from random variation with the same power and significance level. This is not observed power; it is a planning illustration, not a measure of what the completed trial achieved.

The registry’s general note says time-to-event illustrations use total event counts, while other illustrations use participants per arm. The primary endpoint is continuous, so its displayed figures are participants per arm. Planning figures do not establish the trial’s actual recruitment target or the adequacy of its original design, and the record does not report the trial’s original sample-size justification.

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, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = -4.700; pooled standard deviation σ = 11.547.
2. n = 2 × (1.96 + 0.842)² × 11.547² / -4.700² = 94.7, rounded up to 95 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
delta <- -4.7                      # observed difference in means
sigma <- 11.546783634004                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^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 (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(1009138)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 95 (80% power), 127 (90% power)
 75% of observed effect: n per arm = 169 (80% power), 226 (90% power)
 50% of observed effect: n per arm = 379 (80% power), 508 (90% power)
power.t.test: 95.7 
Simulated power at n = 95 per arm: 0.794 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Multiplicity, Missing Data and Analysis Populations

The registry identifies depressive symptoms as the primary outcome and lists a number of secondary outcomes. It does not report a multiplicity adjustment, a hierarchy for testing outcomes, or a statistical plan specifying which comparisons were confirmatory. When several outcomes are tested, the chance of at least one result appearing statistically notable by chance can rise. In general, adjustment methods or a prespecified testing sequence can address that issue, but whether either was used is not reported in the registry record. The secondary p-values should therefore be interpreted as unadjusted, and they carry less confirmatory weight than a result from a fully reported prespecified analysis.

The registry’s analysis count is zero, and the listed secondary outcomes have no reported analyses. The primary numerical contrast described in the posted results is a simple recalculation from group summaries rather than a sponsor-reported formal analysis. The record does not report an analysis population such as intention-to-treat or per-protocol, nor does it explain how participants with missing outcome data were handled. Imputation, complete-case analysis, and sensitivity analyses are not reported in the registry record.

These omissions matter because missing follow-up outcomes can affect both the number of observations contributing to a result and the representativeness of the group summaries. Randomization describes assignment, but it does not tell readers how outcome availability was handled after assignment. The outcome counts in the posted summaries do not, by themselves, explain why they differ from one another or from enrollment.

Interim analyses, stopping rules and details of the formal statistical model are also not reported in the registry record. Without those details, it is not possible to establish whether the posted comparison matches the original planned analysis or whether decisions made during the study affected the reported result. This is a limit on how fully the statistical evidence can be audited from the registry entry, not proof that any particular procedure was or was not used.

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 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: severe hypoglycaemia (6.5%), norwalk-virus (3.7%), ketoacidosis (3.7%), new diagnosis of diabetes long-term complication (2.8%), new diagnosis of cancer (1.9%).

The registry lists serious adverse event counts for 106 participants at risk in the DS-CBT group, with 11 affected, and 108 at risk in the Standard Diabetes Education group, with 21 affected. For other adverse events, the listed counts are 28 in each group, with 106 and 108 at risk, respectively. These are counts as entered in the record; they are not recalculated rates and should not be compared without attention to the recorded groups at risk and the definitions used.

The most frequently listed serious-event terms include Severe Hypoglycaemia at 6.5%, Norwalk-Virus at 3.7%, Ketoacidosis at 3.7%, New diagnosis of diabetes long-term complication at 2.8%, New diagnosis of cancer at 1.9%, and Death at 0.9%. The record does not provide group-specific counts for these terms. The group death fields are not populated, so group-specific death counts are not reported in the registry record.

These safety entries describe reported events; they do not establish that an intervention caused an event or that differences between groups are reliable. The registry record does not report further detail about event definitions, severity grading beyond the serious-event designation, or a comparative statistical analysis. The safety figures should therefore be read as descriptive registry reporting rather than as a causal comparison.

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

The primary posted result describes a larger average decrease in CES-D scores in the DS-CBT group than in the Standard Diabetes Education group over baseline to 12-month follow-up. The unadjusted recalculated mean difference is -4.7 points, and the reported interval is -8.068 to -1.332. This is evidence about a difference in group-average score changes in the posted outcome summaries, under the assumptions of the simple comparison.

It does not show that every participant experienced a decrease, that the group difference was important to patients, or that the result applies to people outside the trial population. The record does not report a threshold for a clinically meaningful CES-D difference. Nor does the result establish which components of the group interventions may have contributed to the observed contrast. The comparator itself included education, group participation, social contact and knowledge acquisition as described in the registry.

The randomized design is relevant because it compares intervention groups formed through random assignment. However, the registry lists no masking, and does not report details of allocation concealment, adherence, attrition, missing-data methods, the analysis population or the sponsor’s formal analysis. Those unknowns limit the conclusions that can be drawn from the registry summaries alone. The recalculated unadjusted comparison should not be mistaken for a comprehensive analysis of the trial.

Secondary results add information about other measured domains but do not automatically confirm the primary finding. Multiple outcomes were listed, and multiplicity procedures are not reported. Differences across instruments can reflect their distinct scales and constructs, so statistical patterns across secondary measures need cautious interpretation.

The result is best understood as a statistical description of the posted primary endpoint: the average score change differed between the groups in the reported summaries, with the estimate favoring a larger reduction in the DS-CBT group. It is not, on its own, a definitive statement about clinical benefit, mechanisms, individual outcomes, safety causation or effectiveness in other settings.

17. Why This Trial Matters Statistically

This trial illustrates why a clinical comparison needs to be read through its endpoint definition, design and analysis together. The outcome is a change in CES-D score, so the sign of the estimate depends on how change is defined. Here, the registry specifies follow-up minus baseline; negative changes indicate lower follow-up scores. Interpreting the contrast without that definition could reverse its meaning.

It also demonstrates the difference between a within-group change and a between-group comparison. Both groups had negative mean changes, but the scientific question concerns whether those changes differed. The recalculated contrast and its interval provide a direct comparison of the group summaries, whereas a change in one arm alone would not account for what happened in the comparator group.

The entry also shows the importance of separating a simple recalculation from a sponsor-reported analysis. The statistical summaries make it possible to describe an unadjusted estimate and its uncertainty, but the registry does not provide a formal analysis plan or reported analysis. That distinction is important for assessing prespecification, covariate adjustment, missing-data handling and the role of secondary endpoints.

Finally, the trial’s multiple outcome domains make multiplicity and endpoint prioritization relevant. A primary result can be interpreted separately, while secondary results should be viewed in light of the number of outcomes and the absence of reported adjustment procedures. The record thus offers a useful example of both what a registry result can communicate and what readers need before making stronger statistical or clinical claims.

18. Limitations

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

Several limitations are specific to the information available for this trial. The registry reports no sponsor analyses, and the primary comparison is a simple unadjusted recalculation from the posted means and standard deviations. The formal statistical model, covariate adjustments and intended analysis population are not reported in the registry record. It is therefore not possible to determine whether the recalculation reproduces the trial’s original planned analysis.

The record does not explain missing outcome data or participant flow between enrollment and the posted endpoint summaries. It lists outcome counts of 93 for DS-CBT and 88 for Standard Diabetes Education, but does not report how unavailable measurements were treated or why the outcome counts differ. The trial’s original sample-size justification is also not reported; the planning illustrations based on the observed effect cannot fill that gap.

The registry identifies multiple secondary outcomes but does not report formal analyses, multiplicity control or an endpoint hierarchy. This limits the confirmatory interpretation of secondary results. The record also does not report a minimum clinically important difference for the CES-D score, limiting interpretation of the primary estimate’s clinical importance.

Masking is listed as none. Further details about allocation concealment, adherence and outcome assessment are not reported in the registry record. The entry describes the population broadly as diabetic patients with subthreshold depression, but does not provide further eligibility or recruitment detail in the information reported. These limitations qualify interpretation of the registry results and should not be replaced by assumptions about procedures that are not described.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Evaluation of a Diabetes-specific Cognitive Behavioural Treatment for Subthreshold Depression — NCT01009138.
• Registry record last updated 2022-10-06; status last verified 2022-09.
• Results first posted 2015-11-26.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

The completed randomized, parallel-group trial compared Diabetes-Specific CBT with Standard Diabetes Education in diabetic patients with subthreshold depression. Masking is listed as none. Enrollment is recorded as 214, with a study start of 2009-11 and primary completion of 2012-03.

The primary endpoint was change in CES-D depressive-symptom score from baseline to 12-month follow-up. The posted group means were -7.4 for DS-CBT and -2.7 for standard education. The unadjusted recalculated mean difference was -4.7, with a 95% confidence interval from -8.068 to -1.332 and p = 0.006. The record lists secondary outcomes, but no formal analyses are reported. Details of the original statistical plan, missing-data handling, and multiplicity procedures are not reported in the registry record.