Experimental Design Planner

Study Design: Brief Mindfulness Meditation and Working Memory in University Students

Design summary: A three-arm, parallel-group, randomized controlled experiment (mindfulness vs. active control vs. passive rest). It uses a baseline-adjusted working-memory outcome, is pre-registered, and has a 24-hour follow-up.

Four problems in the specification as given:

1. It has no baseline working-memory (WM) measurement.
2. The planned active control (nature audio) is probably not inert.
3. The MAAS median split cannot be computed before randomization unless the cutoff is fixed in advance.
4. The automated OSPAN's built-in practice phase would break the "immediately afterward" requirement.

Each is handled below and listed in the final checklist.

1. Frame the Study

Hypotheses

H1 (primary, confirmatory): Among university students, a single 10-minute guided mindfulness meditation produces higher OSPAN partial-credit scores immediately afterward than 10 minutes of passive silent rest, adjusting for baseline OSPAN.

• Contrast: μ_MIND − μ_REST > 0, tested two-sided at α = .05.

H0: μ_MIND − μ_REST = 0. Once baseline OSPAN is adjusted for, adjusted mean OSPAN does not differ between mindfulness and passive rest.

Secondary questions (pre-registered as secondary or exploratory)

Expected direction and why it matters

The expected direction is mindfulness > rest on WM. The proposed mechanism is that focused-attention practice reduces mind-wandering and anxious rumination, freeing executive resources (attentional control theory; the consistent correlation between mind-wandering and WM).

Challenge to the premise: The single-session literature is much weaker than the multi-week training literature. Effects of brief inductions on executive function are small, heterogeneous, and probably inflated by publication bias and small samples. The honest prior is therefore a small effect (d ≈ 0.2–0.4), possibly zero.

This is why the study matters. Students and educators are widely told to "meditate before an exam" on thin evidence. A well-powered, pre-registered test is informative whether the result is positive or null, but only if the design can support a meaningful null (hence the equivalence testing in §5).

2. Define Variables

Independent variable

Pre-task intervention (10:00 min, audio delivered by computer through identical headphones in all arms):

Dependent variables

Primary: Automated OSPAN partial-credit score (0–75)

• Defined as the number of letters recalled in the correct serial position, summed across all 15 sets (set sizes 3–7, three sets of each).
• Administered in E-Prime (Unsworth et al., 2005 paradigm).
• Pre-registered processing criterion: math accuracy ≥ 85%. The primary analysis is intention-to-treat (ITT), with a sensitivity analysis applying this criterion.

Secondary outcomes

• STAI-S (Form Y-1, range 20–100), measured before and after the intervention.
• OSPAN math accuracy and math RT, to check for speed–accuracy trade-offs.

Manipulation and process checks (collected after the OSPAN so the primary outcome stays "immediate"):

• A state mindfulness measure (e.g., State Mindfulness Scale or Toronto Mindfulness Scale).
• A brief credibility/expectancy rating.
• A self-reported dozing item ("Did you fall asleep?").
• An engagement item.

Control variables

These are held constant as specified. Additions:

• The 24-h retest is also run at 2:00–4:00 PM.
• The experimenter leaves the room during the intervention.
• All arms wear headphones.
• Posture and eye instructions are standardized across arms. This matters because body-scan scripts often say "close your eyes." Either allow eyes-closed in all arms or instruct eyes-open in all arms. An eyes-closed/eyes-open difference would confound the comparison through visual input and drowsiness.

Confounders and how each is neutralized

Rationale for adding a baseline OSPAN. Working memory capacity varies enormously between people. Without a baseline, random group imbalances and trait variance swamp a small state effect. OSPAN scores are reasonably stable over time (test–retest correlations are typically moderate-to-high). ANCOVA on baseline therefore reduces error variance by a factor of about (1 − ρ²), which roughly halves the required N at ρ ≈ .7. The cost is one extra visit and a practice effect, which parallel forms and counterbalancing handle, and which is equal across arms by randomization anyway.

3. Conditions and Sampling

Control and treatment arms: two challenges

1. Passive rest is not a neutral baseline. Ten minutes of silent, unstructured sitting is boring and invites mind-wandering and rumination. If MIND > REST, it could mean mindfulness helps or that rest hurts relative to normal functioning. This is exactly why the ACTIVE arm and S3 matter. The interpretation rule should be pre-registered:

• MIND > REST and MIND > ACTIVE → specific mindfulness effect.
• MIND > REST but MIND ≈ ACTIVE → any structured audio engagement helps.

2. A nature documentary is a poor "neutral" control. Attention Restoration Theory predicts that nature content itself restores directed attention, and there is empirical support for restorative effects of nature exposure on attention and WM tasks. A nature audiobook could produce a benefit that masks a real mindfulness effect.

Recommendation: use content that is non-nature, non-emotional, and mildly engaging, such as an excerpt from a history-of-technology or architecture text. Pilot it for neutrality on arousal, valence, and interest ratings. If the team keeps nature audio, label the arm "nature listening" rather than "neutral," and interpret it accordingly.

Stimulus sampling caveat. One meditation recording with one narrator means the study tests that recording, not "mindfulness." If feasible, use two to three scripts per active arm and treat script as a random factor. At minimum, acknowledge this limit to generalizability.

Design type: three-arm between-subjects parallel RCT, baseline-adjusted

A within-subjects crossover would be more powerful, but it is rejected for three reasons:

• Asymmetric carryover: participants cannot "unlearn" mindfulness instructions and may apply them during later rest sessions.
• Unblinding: experiencing all three arms reveals the hypothesis.
• Practice effects: OSPAN performance improves through strategy acquisition, and a crossover needs four or more equivalent forms.

The between-subjects design with a baseline covariate recovers much of the crossover's efficiency without these problems.

Population

Undergraduates aged 18–25 at Riverton State University, per the stated inclusion and exclusion criteria.

Additions:

• Normal or corrected hearing and vision.
• Not a psychology student who has completed coursework covering OSPAN or mindfulness research. This is optional but reduces hypothesis guessing.
• Record recruitment channel (course-credit pool vs. paid). These groups often differ in motivation.

Sample size

Primary contrast: MIND vs. REST, two-sided α = .05, power = .80. The ANCOVA adjustment factor is (1 − ρ²), where ρ is the correlation between baseline and post-intervention OSPAN.

Formula: n per arm ≈ 2(z₁₋α/₂ + z₁₋β)² / d² × (1 − ρ²)

Recommendation: target d = 0.30 with ρ = .60 (conservative, since forms and days differ), giving 112 per arm.

• Add about 2 per arm for covariate degrees of freedom.
• Add about 10% for post-randomization loss (technical failure, math-accuracy exclusions in sensitivity analyses, 24-h dropout).
• Target: 125 per arm, N = 375 randomized.

Why not d = 0.5? Powering for a medium effect would be the standard default, but it is not justified by the brief-induction literature. A study with 40 per arm has less than 50% power to detect d = 0.3 and would add another uninformative small study to a biased literature.

If N = 375 is infeasible at one site, choose one:

• (a) A group-sequential design with one interim analysis at 50% of the sample and O'Brien–Fleming boundaries. This allows early stopping for efficacy or futility.
• (b) Multi-site collaboration.
• (c) Explicitly power for d = 0.40 (about 70 per arm, N ≈ 210) and state in the pre-registration that effects below 0.40 cannot be reliably detected.

Secondary power, stated honestly:

• The Condition × MAAS interaction needs roughly 4× the main-effect N for a comparable effect size. S1 is exploratory and is reported with confidence intervals, not as a confirmatory test.
• The S3 equivalence test (bounds ±0.30) at 112 per arm has adequate power only if the true difference is near zero. Pre-register it with this caveat.
• Run a sensitivity power analysis (minimum detectable effect at the achieved N) and report it.

Randomization and allocation concealment

• Stratified block randomization. Strata are MAAS high/low crossed with sex, if desired. Use randomly permuted block sizes of 3 and 6 instead of a fixed 6, because fixed blocks let the final allocations in each block be predicted.
• The MAAS cutoff problem. A "median split" cannot be computed before the sample exists. Fix the cutoff in advance using a pilot sample or published student norms, and pre-register the numeric value. Collect MAAS at screening, before randomization.
• Concealment. Prefer a centralized electronic system (REDCap randomization module) over sealed envelopes. Envelopes can be opened early, reordered, or held up to light. If envelopes are used, they should be sequentially numbered, opaque, and tamper-evident, and each opening should be logged with the participant ID and timestamp.
• Timing. Randomize at Session 2 arrival, after eligibility re-checks (sleep, caffeine). This minimizes post-randomization exclusions.

Blinding: what is actually achievable

• Participants cannot be blind to what they did. The "comparing relaxation techniques" cover story partially masks the hypothesis. However, mindfulness is not relaxation, and the framing primes all three arms to expect relaxation. It is also mild deception, so the IRB must approve it and the debrief must address it.
• Measure credibility and expectancy, and test whether expectancy differs across arms or predicts OSPAN. Expectancy cannot be removed, only measured.
• The experimenter is the real blinding risk. OSPAN is scored automatically, so blinding the "scorer" adds little. The bigger risk is the experimenter's behavior before and after the intervention.
  • Mitigations: E-Prime launches the audio from the allocation code; the experimenter sets up, leaves the room, and returns only at an auto-triggered prompt; all instructions are scripted.
  • Ask the experimenter to guess each participant's allocation, as a check on how well their blinding held.
• The analyst is blinded. Arms are coded A/B/C, and the analysis script is locked and time-stamped (on OSF) before unmasking.

4. Procedure and Measurement

Protocol

Session 0: online screening (~15 min)

1. Electronic consent for screening.
2. Eligibility questionnaire (age, language, health, medication, meditation history).
3. MAAS, demographics, chronotype, habitual caffeine and nicotine use, exam schedule.
4. Eligible participants are invited to the lab.

Session 1: lab baseline (~40 min), 2–7 days before Session 2, 2:00–4:00 PM

1. Written informed consent.
2. Full OSPAN instruction and practice phases (letter-only, math-only with individual time-limit calibration, combined).
3. Baseline OSPAN on Form X (Latin-square assigned).
4. Scheduling for Sessions 2 and 3.

Session 2: intervention (~50 min), 2:00–4:00 PM

1. Arrival check: sleep hours, caffeine/nicotine/alcohol, Stanford Sleepiness Scale. Reschedule if criteria are not met.
2. Randomization via REDCap.
3. Brief OSPAN refresher practice (about 3 trials) and re-calibration of the math time limit. This deliberately happens before the intervention, so that the post-intervention OSPAN begins with test trials. Otherwise the standard ~10-minute practice block would sit between the intervention and the outcome.
4. STAI-S (pre).
5. Scripted instructions. Headphones on. The experimenter exits. The 10:00 intervention plays.
6. STAI-S (post), about 3 minutes, identical position in all arms.
7. OSPAN test trials on Form Y (about 15–20 min).
8. Post-task: manipulation check (state mindfulness), credibility/expectancy, engagement, dozing item, a free-text "what do you think the study was about?", and the experimenter's guess of allocation.

Session 3: 24-hour follow-up (~30 min), 22–26 h later, 2:00–4:00 PM

1. Same arrival checks.
2. No intervention. STAI-S.
3. OSPAN on Form Z.
4. Full debrief: true purpose, rationale for the cover story, counseling resource list, option to withdraw data.
5. Compensation.

Timing caveat. A roughly 3-minute gap for the STAI plus a 15–20 minute task means "immediately" is really "0–25 minutes post." Pre-register an exploratory analysis of the effect by OSPAN half (sets 1–8 vs. 9–15) to capture decay within the task. If the "immediate" window is the main theoretical interest, consider moving the STAI-post to after the OSPAN, accepting that it will then be contaminated by the task.

Theoretical caveat on S2. A lasting WM benefit 24 h after a single 10-minute session, with no practice in between, is not well motivated theoretically. The expected result is null. S2 is useful mainly to rule out claims of lasting benefit.

Instrument reliability and fidelity checks

• OSPAN: report in-sample split-half reliability (Spearman–Brown corrected) of partial-credit scores at each time point.
• Form equivalence: pilot all three forms (n ≈ 30, within-subjects, counterbalanced) to check that means are comparable before the main study. In the main study, include form as a covariate. Unvalidated parallel forms are an invalidation risk (see flags).
• Questionnaires: report Cronbach's α or McDonald's ω for STAI-S and MAAS in-sample.
• Fidelity:
  • Audio playback logged by E-Prime (start and end timestamps).
  • Experimenter adherence to the script, audited on a 10% random sample of sessions via checklist.
  • Room temperature and noise logged each session.
• Data quality: E-Prime files are auto-exported, double-checked against the participant log, and totals are recomputed by the analysis script, not entered by hand.

5. Statistical Analysis Plan

All analyses are pre-registered on OSF before data collection. A Registered Report format is strongly recommended given the file-drawer problem in this literature. Data, code, and materials (including the audio scripts) are shared openly.

Primary analysis

ANCOVA on Session 2 OSPAN partial-credit score:

OSPAN_post ~ Condition + OSPAN_baseline + MAAS stratum + Form_post

• Planned contrast for H1: MIND vs. REST, two-sided α = .05. This is the only confirmatory test, so no correction is needed for it.
• Analysis population: ITT (everyone randomized who has post-intervention data).

Assumption checks and fallbacks:

Secondary analyses (Holm–Bonferroni within this family)

1. S3: MIND vs. ACTIVE contrast. Also a TOST equivalence test with SESOI d = ±0.30; confirm or revise this SESOI before registration. Report ACTIVE vs. REST descriptively.

2. S2: Linear mixed model for OSPAN at post and 24 h:

   OSPAN ~ Condition × Time + Baseline + Form + (1 | participant)

   This model uses all available data under a missing-at-random assumption. Add a sensitivity analysis using multiple imputation and a pattern-mixture (delta-adjustment) model for 24-h dropout.

3. S4: STAI-S post, analyzed by ANCOVA with STAI-S pre as covariate.

Exploratory analyses (no correction; labelled as hypothesis-generating)

• S1 moderation: Condition × MAAS (continuous) on OSPAN_post; simple slopes at ±1 SD; Johnson–Neyman intervals. A median-split plot is included for readers, but inference comes from the continuous model.
• Mediation: Condition → ΔSTAI → OSPAN, with bootstrap indirect effects. This is causally weak, because the mediator and outcome are measured close together and are not independently manipulated. Label it accordingly.
• Expectancy: add credibility/expectancy as a covariate and check whether the effect survives.
• Within-task decay: effect in the first vs. second half of the OSPAN.
• Per-protocol sensitivity: exclude math accuracy < 85%, self-reported dozing, and protocol deviations.

Effect sizes and reporting

• Adjusted mean differences in raw OSPAN units with 95% CIs. Raw units are interpretable (for example, "+2.1 letters").
• Standardized d computed using the pooled post-test SD, not the ANCOVA residual SD, which inflates d. State the method explicitly.
• Partial η² for the omnibus test.
• A Bayes factor for H1 (JZS prior, r = 0.707, plus sensitivity to the prior width). This lets a null result be read as evidence for H0 rather than as mere absence of evidence.
• CONSORT flow diagram and CONSORT-style checklist.

6. Ethics and Threats to Validity

Ethics

The stated plan is adequate. Additions:

• Deception: the "relaxation techniques" cover story is deception by omission. The IRB application must justify it, and the debrief must offer data withdrawal.
• Consent staging: separate consent for the online screening (which collects health and medication data) from consent for the main study.
• Distress protocol: STAI-S is a state measure, not a clinical screener. Still, pre-specify what the experimenter does if a participant appears distressed, and if any item or score triggers concern. Provide counseling resources to all participants, not only those with high scores.
• Adverse reactions to meditation: these are rare but documented, particularly body-scan-induced anxiety or dissociation in people with trauma histories. Mention this in the consent form, include a "stop anytime" instruction, and log adverse events.
• Course-credit coercion: offer an equivalent non-research alternative for credit.
• Data: de-identified IDs; linkage key stored separately from data; retention period stated; open data released only after verification that re-identification is not possible from demographics.

Threats to validity

Rationale for Major Choices

Three-arm design. A mindfulness-vs-rest comparison alone cannot distinguish a mindfulness-specific benefit, a generic benefit of structured auditory engagement, and a decrement caused by ten minutes of boredom. The active arm turns an ambiguous result into an interpretable one. It costs 50% more participants, which is justified because S3 is the question reviewers and practitioners will ask first.

Between-subjects with a baseline covariate instead of a crossover. Mindfulness instructions produce irreversible and asymmetric carryover, and repeated exposure to all arms reveals the hypothesis. Adding a baseline OSPAN recovers much of the crossover's statistical efficiency (a (1 − ρ²) variance reduction) without these costs.

Powering for d = 0.30. The main risk to this study's value is not a false positive but an uninterpretable, underpowered null added to a literature already distorted by small studies. Powering for a realistic small effect, together with equivalence testing and Bayes factors, makes both outcomes informative. If resources force a smaller N, the team should explicitly state the minimum detectable effect rather than silently adopt d = 0.5.

Continuous MAAS instead of a median split for inference. Dichotomizing a continuous moderator discards information, reduces power, and makes results depend on the sample. Keeping the split for stratification is harmless and helps balance. Inference, however, should use the full MAAS distribution.

Moving OSPAN practice before the intervention. The standard automated OSPAN places roughly 10 minutes of practice and calibration directly before the test trials. Running it after the intervention would stretch the gap to "immediately afterward" beyond 10 minutes and dilute any transient state effect. Full practice happens at baseline, and only a brief refresher and calibration occur before the intervention in Session 2.

Single confirmatory test. Designating MIND vs. REST as the only confirmatory contrast keeps α = .05 for the research question as stated. Secondary comparisons are controlled with Holm correction, and exploratory work is clearly labelled. This avoids both an over-conservative blanket Bonferroni correction and uncorrected fishing.

Assumptions That Could Invalidate the Results

1. 🚩 The "neutral" active control is actually restorative (nature content under Attention Restoration Theory). This would mask a true mindfulness effect and lead to a false "no specific effect" conclusion for S3.
2. 🚩 Passive rest is treated as neutral. If rest harms performance, a MIND > REST result reflects a control decrement, not a benefit. The active arm and pre-registered interpretation rules are the defense.
3. 🚩 The OSPAN parallel forms are assumed equivalent. If they are not, and form assignment is imbalanced by chance, form effects can masquerade as condition or time effects, especially for S2. Pilot the forms and include a form covariate.
4. 🚩 Effect-size optimism. Powering for d ≥ 0.5 would make a null result uninterpretable and a positive result likely inflated.
5. 🚩 The MAAS median must be fixed before randomization. A cutoff computed from the eventual sample would make stratification impossible or post hoc.
6. 🚩 Expectancy is treated as controlled by the cover story. It is not. If expectancy differs by arm and predicts OSPAN, the causal claim weakens. It must be measured.
7. 🚩 Post-randomization exclusions (math accuracy, dozing, failed manipulation checks) applied in the primary analysis can break randomization and bias the estimate. Keep ITT as the primary analysis.
8. 🚩 Ceiling effects in a university sample could compress any real effect. Pilot the score distribution.
9. Self-reported sleep and caffeine are unverifiable. The rescheduling policy limits but does not eliminate this problem.

Decision Checklist (confirm before pre-registration)

• Active control content: replace the nature documentary with non-nature neutral content, or keep it and relabel the arm?
• Meditation history: exclude (as in the inclusion criteria) or stratify (as in the confounder list)? These are currently contradictory. Recommendation: exclude weekly+ practice and record lifetime hours as a covariate.
• Add a baseline OSPAN session (Session 1)? Strongly recommended. It is required for the power calculations above.
• Target N: 375 (d = 0.30), about 210 (d = 0.40 with stated limits), or a group-sequential design? Is recruitment capacity at Riverton State realistic for either?
• Pre-specified MAAS cutoff value for stratification (pilot data or published norms).
• SESOI for the equivalence test (proposed d = 0.30, or a raw-unit value such as ±2 letters).
• Eyes open or eyes closed, standardized across all arms.
• STAI-post position: immediately post-intervention (adds about 3 minutes before OSPAN) or after OSPAN (contaminated by the task)?
• Full STAI-Y1 or the 6-item short form (shortens the gap before OSPAN)?
• Number of scripts per arm (1 vs. 2–3 for stimulus sampling).
• Randomization platform: REDCap vs. sealed envelopes; variable block sizes (3/6).
• Form-equivalence pilot (n ≈ 30) scheduled and budgeted.
• Ceiling policy: the threshold that would trigger switching to a harder span task.
• Per-protocol exclusion rules written out verbatim (math accuracy < 85%, dozing, deviations).
• Compensation structure for three sessions: is $15 still adequate? Should it be prorated to reduce 24-h attrition?
• Registered Report submission vs. standard OSF pre-registration.
• IRB approval of deception (the cover story) and the adverse-event protocol for meditation.
• Exam calendar checked to exclude midterm and finals weeks from data collection windows.