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Alan M. Zaslavsky develops statistical methods for measuring health-care quality and disparities. His research includes missing data, hierarchical Bayesian models and Bayesian inference, bringing statistical adjustment to comparisons between health-care providers and populations.^[ref]

With Fan Li and Kari Lock Morgan, he developed a framework for balancing covariates through propensity score weighting. Their overlap weights emphasize people with a substantial chance of receiving either treatment, defining an overlap-weighted average treatment effect for that comparison population.^[ref]

A recorded variable included in imputation models to help predict missing values or explain response patterns, even if it is absent from the final substantive model. Useful auxiliaries can improve precision and make missing at random more plausible; they cannot establish that assumption from the observed data.

Donald Rubin's work connects Causal inference, missing data and Bayesian statistics. His Harvard profile lists Causal inference in experiments and observational studies, nonresponse in sample surveys, and Bayesian and empirical Bayesian methods as research interests.^[ref]

The potential outcomes framework makes a causal comparison explicit by distinguishing the outcomes that would occur under alternative treatments. Only the outcome under the received treatment is observed for each individual, so identifying an average treatment effect requires design or modelling assumptions. In missing-data analysis, multiple imputation propagates uncertainty by analyzing several completed datasets and pooling their results with Rubin's rules. These ideas explain why filling in one convenient value and then treating it as observed generally understates uncertainty.

Homepage: statistics.fas.harvard.edu/people/donald-b-rubin

A table of category counts, often accompanied by sample proportions or percentages. Its denominator must be stated, especially when observations contain missing data.

An intention-to-treat analysis compares participants according to their randomized assignment, retaining that assignment even when they do not use the assigned intervention. Its causal effect is the effect of assignment under the study's actual adherence pattern, rather than the effect of perfect adherence. Randomization protects this comparison from baseline confounding; missing data can still require assumptions or additional analysis.

For monotone missing data, let $R_{ij}$ indicate observation and let ${\rho }_{ij}$ be the product of the conditional retention probabilities through visit $j$. Under sequential missing at random, conditioning on the complete response history makes these retention probabilities depend only on the history already observed at each decision. Therefore $\mathbb{E}(R_{ij}/{\rho }_{ij}\mid Y_i,X_i)=1$. Weighting a working-independence generalized estimating equation by $R_{ij}/{\rho }_{ij}$ restores its mean-zero property. This needs correct retention probabilities, positivity and regularity; uncertainty must account for estimating the weights.

John Carlin develops biostatistics for health and medical research, including methods for missing data and causal inference. His institutional profiles describe work on multiple imputation and the need to specify the scientific purpose of an analysis before choosing a regression model.^[ref][ref]

With multiple imputation, several plausible completed datasets represent uncertainty about unobserved values. Their analyses must account both for uncertainty within a completed dataset and for variation between completed datasets. This makes the assumptions about the missing values visible in the analysis. Carlin is a coauthor of Bayesian Data Analysis by Andrew Gelman and others.^[ref]

Data are missing completely at random when the missingness indicator is independent of both observed and missing data.

Missing data are intended measurements that were not observed. Write $R=1$ when an outcome $Y$ is observed and let $X$ denote fully observed covariates. The observation mechanism matters because observed cases can differ systematically from the target population.

Missing completely at random means $R$ is independent of both $Y$ and $X$. Missing at random allows observation to depend on $X$, but requires $R$ and $Y$ to be conditionally independent given $X$. Missing not at random permits additional dependence on the unobserved $Y$. For example, follow-up determined only by recorded age can be missing at random after conditioning on age; follow-up depending on unrecorded current symptoms can be missing not at random. The missing-at-random assumption generally cannot be established from the observed data alone.

An observed-case analysis need not estimate the population mean even under missing at random, because the distribution of $X$ among observed cases can be different. Regression, Inverse probability weighting or Multiple imputation can address this under suitable assumptions, including a positive probability of observation throughout the target population. Stating those assumptions is part of the statistical model rather than a consequence of an imputation algorithm.

Suppose an endpoint is binary, $N$ people are in the target cohort, $r$ observed outcomes are successes and $m$ outcomes are missing. With no assumptions about the missing values, the cohort success proportion $p$ satisfiesFor the proof, let $u$ be the number of successes among the missing outcomes. Since $0\le u\le m$ and $p=(r+u)/N$, both inequalities follow. Every integer $u$ in that range is a possible completion of the observed data, so the endpoints are sharp. These are missing data bounds on a cohort proportion, not confidence intervals or bounds on a causal treatment effect.

Repeated measurements have a Monotone missing-data pattern when every measurement after a subject's first missing value is also missing.

Multiple imputation repeatedly draws missing values from fitted predictive distributions, including uncertainty about fitted parameters, analyzes each completed dataset, and combines the resulting estimates and uncertainty.

Routine outcome monitoring has made the results of IAPT services unusually visible and has created opportunities to improve care. Its benefits should be separated into three claims: measurement is more complete, the resulting information supports clinical and organisational decisions, and acting on that information improves patient outcomes. The first two do not automatically prove the third. A service can record a recovery accurately without the act of recording being its cause.

The historical IAPT programme expanded psychological treatment for depression and anxiety, using evidence-based interventions and stepped care where appropriate. Repeated measures allow a trajectory to be examined instead of relying on a clinician's general impression at discharge. Depression, general anxiety and disorder-relevant symptoms can be monitored alongside functioning and the person's own goals. A symptom questionnaire is a useful indicator, but a cutoff-based service definition of recovery is not identical to a blinded diagnostic interview or to complete restoration of everyday life.

David M. Clark and colleagues' evaluation of the Doncaster and Newham demonstration sites showed that session-by-session collection could achieve unusually complete before-and-after information in routine care. Reported recovery was about 55–56% among patients seen at least twice, and a follow-up examined maintenance beyond the last session. These prospective service cohorts demonstrated feasibility and informed implementation, but were not randomised tests of monitoring itself. Their denominator also excluded people who never progressed beyond an initial contact.^[ref]

Completeness matters because selective follow-up can substantially distort apparent success. Consider a purely hypothetical cohort of one hundred baseline cases: fifty have an endpoint recorded and thirty of those meet the chosen recovery criterion. The observed-case recovery rate is 60%. If none of the fifty missing cases recovered, the whole-cohort rate is 30%; if all recovered, it is 80%. The missing-outcome bounds for a binary endpoint are sharp: both extremes fit exactly the observed data. Without assumptions or additional measurements, the observations alone cannot identify where within those bounds the cohort lies. This example is not an estimate of any IAPT service.

Sessional collection reduces dependence on a separate final questionnaire: a last available observation often exists even when a planned final appointment is missed. It does not make all missingness harmless. A last attended session can occur earlier for someone who disengages, and is not automatically equivalent to a common long-term endpoint. Outcomes should therefore be reported with clear eligibility, timing, completion and missing data definitions. Monitoring treated patients very thoroughly still does not describe those who were referred but never entered treatment.

David M. Clark and colleagues' 2018 analysis reported approximately 98% before-and-after symptom coverage among treated IAPT patients. It related public service outcomes to organisational characteristics and examined whether those characteristics also predicted changes between years. Waiting, missed appointments and the organisation of treatment were associated with outcomes; deprivation remained relevant. This made variation actionable and generated specific implementation hypotheses. Nevertheless, service-level associations and longitudinal prediction remain vulnerable to case mix, selection and unmeasured organisational differences.^[ref]

At the individual level, a visible trajectory can identify deterioration or lack of progress earlier than an end-of-treatment assessment. This provides a reason to review the formulation, barriers, intervention fidelity or level of care. It can make supervision concrete: a supervisor and therapist can examine which patients are not improving and whether the active treatment has actually been delivered. A score should initiate inquiry rather than automatically trigger a uniform decision, since transient distress, measurement error and contextual crises can change a session's result.

There is experimental evidence for an additional feedback system. Jaime Delgadillo and colleagues randomised therapists to automated outcome feedback or usual psychological treatment across eight NHS trusts. Seventy-seven therapists participated and 2233 patients were included. The system flagged people who were not on track and prompted supervisory review. Among those classified as not on track, feedback was associated with modestly better depression and anxiety outcomes, with effect sizes around 0.23 and 0.19 respectively. The trial tested feedback and its linked clinical response within services already collecting measures, not questionnaire collection versus no monitoring.^[ref]

This distinction is central to interpreting the benefits. Data make a problem detectable; feedback makes it salient; a feasible clinical action must then address it. An alert that repeatedly identifies nonresponse without available treatment alternatives may add burden without improvement. Cluster allocation appropriately recognises that therapists change their practice across patients, while open-label delivery and quasi-random patient allocation to available therapists still qualify the causal interpretation. The modest subgroup effects should not be presented as proof that monitoring transforms every case.

At service level, routinely available outcomes support accountability, training evaluation and investigation of inequalities. Comparisons can identify where referral pathways, waiting times or treatment delivery need examination. However, unadjusted league tables can penalise services treating more complex or disadvantaged populations. Risk adjustment should be transparent and should not erase the very inequalities that require attention. Process measures, symptom outcomes, functioning and reach together give a fuller picture than one recovery percentage.

Targets can also create incentives to select easier cases, change denominators or emphasise crossing a threshold over a person's priorities. A reliable change index scales change by expected measurement error. Reliable improvement distinguishes such a change from a small numerical movement, while reliable recovery additionally considers caseness; neither removes the need to monitor deterioration and residual disability. Questionnaire accessibility, language and the validity of comparing groups require attention. Patients should understand why information is collected and how it contributes to care.

By May 2022, the clearest benefits were high outcome coverage, a transparent basis for improving implementation and a modest experimentally supported benefit from targeted feedback. Routine data had narrowed the gap between trial evidence and what services actually achieved. Further progress required responding intelligently to trajectories, preserving inclusive denominators and testing organisational changes, rather than treating measurement or a rising aggregate recovery figure as self-validating evidence of effectiveness.

A psychological treatment has a specific effect only relative to a clearly defined alternative explanation. Benefit beyond waiting is different from benefit beyond credible therapeutic contact, and both differ from evidence that a named technique works through its proposed mechanism. No single research design establishes all three. A persuasive programme combines controlled clinical comparisons with component and process experiments, while keeping patient-relevant outcomes central.

An uncontrolled before-and-after study cannot isolate a treatment effect. People may enter care when symptoms are unusually severe, creating regression toward their longer-term level; difficulties can improve naturally; expectations, concurrent care and repeated assessment can also change outcomes. A waiting-list randomised trial controls some time-related explanations but adds unequal expectations and contact. It can establish benefit from being offered the treatment package compared with waiting under those conditions, without identifying which ingredient produced the difference.

For specificity beyond nonspecific therapy effects, use a randomised comparison with a credible active intervention. Match time, attention, therapist competence and assessment opportunities as far as the question permits. Measure credibility and expected benefit rather than assuming equivalence from similar session counts. Keep relevant usual care available in both arms. Allocation concealment prevents recruitment decisions from anticipating the next assignment, while blinded independent outcome assessment reduces a different source of bias after allocation. Therapists and patients usually cannot be fully blinded to psychological procedures.

Daniel Freeman and colleagues' Feeling Safe trial illustrates this stronger package comparison. Patients with persistent persecutory delusions received the programme or befriending delivered by the same therapists, alongside usual care. At six months, the primary continuous conviction measure favoured Feeling Safe. This supports an effect beyond the particular befriending comparator, but does not establish that each module is necessary or that the whole benefit travelled through one nominated mediator.^[ref]

The comparator should be interpreted fairly. A weak or implausible control can exaggerate apparent specificity, while an active comparator may itself change the proposed mechanism. If befriending improves social confidence, it is not a biologically inert placebo. A null result may mean two useful treatments have similar effects, both are ineffective, or the study is too imprecise. Failure of a superiority test does not demonstrate equivalence; an equivalence or noninferiority question requires prespecified clinically justified margins and appropriate precision.

A dismantling trial varies a specified component while keeping the surrounding treatment adequate and similar. For example, compare the same exposure programme with and without a safety behavior intervention. This estimates a conditional contribution: absence of an additional benefit does not imply that the component is useless in every context, because another part may produce similar learning. A factorial design can independently vary an action and its explanatory rationale, estimating their effects and interaction when the study has adequate power.

The early panic safety behavior experiment provides both an example and a caution. Greater change after brief exposure with precautions reduced supports the combined manipulation. Yet behavioral instructions and the explanation of the exercise were not fully separated. The appropriate next test would vary those elements independently and check actual behavior and expectancy change. Simply renaming the conditions 'cognitive' and 'behavioral' would not remove the confounding.^[ref]

A mechanistic experiment can provide more direct leverage than a full treatment comparison. Colin MacLeod and colleagues trained attentional bias using a modified dot-probe task and tested later responses to stress. This asked whether experimentally changing information processing altered emotional vulnerability. It remains necessary to establish that the manipulation engaged the intended process rather than only a task-specific strategy, and that any effect transfers to the clinical phenomenon of interest. Laboratory emotional vulnerability is not itself diagnostic remission.^[ref]

Likewise, Daniel Freeman and colleagues used virtual social environments to compare exposure against threat testing with safety behavior reduction. Both groups encountered graded situations, making the content of learning more directly investigable than in a therapy-versus-waiting comparison. The combined manipulation and brief follow-up constrain the mechanism claim. A useful manipulation check, an independent behavioral outcome and later transfer assessment strengthen the design more than a treatment label does.^[ref]

Mediation analysis is informative but insufficient on its own. Randomising treatment identifies the total effect of assignment under the trial's assumptions; it does not automatically randomise the mediator. Symptom improvement could change reported beliefs, or an unmeasured process could influence both the belief score and the outcome. Measure the proposed mediator before the downstream outcome, assess competing pathways and perform sensitivity analyses. Replication using a different way to alter the same process can provide converging evidence; stronger identification may require experimental manipulation of that process itself.

Clinical trials also need suitable sampling, prespecified outcomes, adequate power, intention-to-treat analysis and transparent missing data handling. Outcomes should include functioning and possible deterioration, with follow-up long enough to distinguish transient reassurance from durable benefit. Treatment fidelity and competence must be assessed in both arms. Therapist allegiance, clustering of patients within therapists and differential dropout can affect interpretation. Statistical significance alone does not establish a meaningful improvement, especially when many outcomes or subgroup comparisons are explored.

Pragmatic implementation trials answer a complementary question: does the intervention add benefit in ordinary care, at acceptable cost and burden? Jaime Delgadillo and colleagues' therapist-cluster trial tested an automated feedback system linked to supervisory review within routine services. Its comparison isolates the added feedback arrangement more closely than an observational association between high-performing services and monitoring. It still tests a specified package of information and response, rather than an abstract effect of measurement divorced from clinical action.^[ref]

The strongest conclusion consequently states its level of specificity. A well-conducted active control trial can establish an incremental treatment-package effect. A dismantling or factorial trial can identify a component's contribution within a defined context. An experimental process manipulation, supported by temporally ordered measurements and converging clinical evidence, can constrain the mechanism. Keeping these claims separate prevents a successful therapy from being treated as proof of its entire theory, while preserving the practical importance of improvements patients actually experience.

A frequency table describes category counts and their relative frequencies. The full-sample percentage uses every listed case as denominator; a valid percentage excludes missing data for that variable. A cumulative percentage adds the valid percentages up to an ordered category. The denominator matters as much as the number: a statement about respondents with recorded use need not describe every respondent.

Employment is a binary categorical variable: 1216 cases are employed and 837 are not, or about $59.23\%$ and $40.77\%$. Neither employment category is missing in this output. Employment labels have no intrinsic numerical spacing; codes zero and one identify the two categories under a chosen ordering convention. Cumulative percentages for a nominal categorical variable depend on the arbitrary display order and add little to this two-category description.

Age groups are an ordinal categorical variable because their intervals have a natural ordering, although the grouped representation loses exact ages. Among the five visible age rows, ages 25–44 form the largest group, with $562/1730\approx 32.49\%$, and ages 14–24 the smallest, with $182/1730\approx 10.52\%$. The other visible groups account for $20.98\%$, $16.42\%$ and $19.60\%$ on that denominator. About $43.01\%$ of the visible five-row count is below 45. These percentages should not be silently applied to the stated total $2053$: for example, the same $562$ cases are only $27.37\%$ of $2053$.

The age variable key advertises six categories, whereas only five appear. Their counts sum to $1730$, leaving a difference of $323$ against the printed total; the table nevertheless prints zero missing values. This is an internal source discrepancy, not permission to label those $323$ cases as a particular unseen age group or as recorded missing data. The oldest row is labelled 65+ here but 65–74 in Figure 2. Even the age percentage total has a small display discrepancy: the five rounded percentages sum to $100.01\%$, while the printed valid total and last cumulative percentage say $99.99\%$. The much larger count inconsistency remains after allowing ordinary rounding.

Social media use is also an ordinal categorical variable. Its six ordered categories express increasing frequency, not equally spaced measurements: averaging category labels or claiming a one-unit change has a constant time meaning would require an additional scoring convention. Among the $1424$ observed responses, the mode is never, at $459/1424\approx 32.23\%$, followed by daily, at $28.37\%$. Weekly use accounts for $18.19\%$, use more than once a day for $11.38\%$, less-than-monthly use for $6.39\%$, and monthly use for $3.44\%$. The first three categories together comprise about $42.06\%$ of valid responses. Consequently the middle ordered response lies in the weekly category: cumulative frequency first passes one half there.

Combining the two daily categories gives $566/1424\approx 39.75\%$ of valid responses using social media at least daily. The same recorded responses are $566/2053\approx 27.57\%$ of all listed cases. The second percentage is the fraction recorded as daily users, not an estimate that classifies all missing responses as nonusers. Missing social media responses make up $629/2053\approx 30.64\%$. The directly calculated valid fraction is $69.36\%$; summing the individually rounded full-sample percentages produces the printed $69.37\%$, a minor rounding difference. With no account of the missing-data mechanism, the observed valid distribution should not automatically be generalized to those with missing use. Employment being fully observed does not make social media missingness ignorable. The substantive distributional summary must retain both the valid-response denominator and the missing-data qualification.

The independence analysis is not justified without further assumptions. Three binary responses from the same subject generally remain correlated after conditioning on baseline covariates and treatment. The fitted independent-Bernoulli likelihood discards that correlation and gives incorrect model-based standard errors and tests if it is present. Positive within-subject correlation commonly makes those errors too small.

There is an important distinction between estimating the mean and estimating uncertainty. If the stated marginal logistic regression is correct and responses are fully observed, the independence score ${\sum }_{i,j}{w}_{ij}(Y_{ij}-m_{ij})$ still has zero expectation. With independent subjects and regularity, its root can consistently estimate marginal coefficients despite within-subject dependence; a subject-level sandwich covariance matrix is then needed. True independence is a special case in which the original standard errors would be appropriate.

Dropout creates a separate issue. Restricting that score to observed responses need not preserve its zero expectation if observation depends on the response history or unseen depression outcomes. Therefore both point estimates and uncertainty may be wrong. Neither random treatment assignment nor baseline adjustment alone establishes an ignorable missingness mechanism. We need a model matched to the scientific estimand and explicit assumptions about missing data.

Multiple imputation by chained equations specifies one conditional distribution for each incomplete variable. In general, let $V_1,\dots ,V_q$ be the incomplete variables, $Z$ the fully observed predictors, and ${\varphi }_j$ the parameters of a model $p_j(V_j\mid V_{-j},Z;{\varphi }_j)$. The notation $V_{-j}$ means all variables except $V_j$. The models should respect each variable's support and contain the terms needed by the planned analysis.

First choose suitable models and initialise only the missing entries with admissible provisional values. One sweep updates $j=1,\dots ,q$ in turn. At update $j$, fit its model to records whose $V_j$ is observed, using the latest filled-in predictors. DrawThe first draw represents parameter uncertainty through a Bayesian posterior; the second represents residual uncertainty through a posterior predictive distribution. Replace the missing entries with these draws, leaving every genuinely observed entry fixed. Repeat whole sweeps until the chain has settled, assessing traces, mixing and plausibility. Obtain $M$ completed datasets from independently initialised chains, or sufficiently separated draws after convergence. Both parameter and missing-value uncertainty must be propagated; repeated deterministic prediction is not multiple imputation.

Here use a logistic regression for $C$ conditional on $P$, age and sex. For $P$, use an appropriate discrete count model conditional on $C$, age and sex, such as a suitably checked negative binomial regression, allowing enough flexibility for skewness and nonlinear effects. Include interactions or transformations needed by the analysis in the imputation models. If condom use is structurally undefined for a record, preserve that applicability rule rather than treating it as ordinary missing data.

Impute the eligible survey information before discarding records solely because the observed $P$ is absent. In each completed dataset select its own $P>1$ records and fit the requested logistic regression. This allows a record with missing $P$ to contribute to the target group in some imputations and not others. Models must respect any known eligibility restrictions; if eligibility was independently known, use that information.

For a scalar regression coefficient, let ${\hat{Q}}_m$ be its estimate and $U_m$ its estimated variance in completed dataset $m$. Rubin's rules giveThe standard error is $\sqrt{T}$. Use the corresponding multiple-imputation confidence interval, rather than treating one completed dataset as fully observed. For vector coefficients replace the squared differences by outer products and $U_m$ by the covariance matrix. This combines within-imputation and between-imputation uncertainty.

Perioperative care is the coordinated care surrounding surgery: before the operation, during it and through recovery afterward. It connects the decision to operate with preparation, the conduct of the procedure and subsequent assessment of recovery and complications. NICE’s enhanced-recovery recommendation explicitly includes preoperative, intraoperative and postoperative components.^[ref]

Before an operation, relevant work includes assessing the person and procedure, communicating likely benefits and risks and supporting informed consent. During the operation, anaesthesia, physiological measurements and the surgical intervention must be coordinated. Afterward, responsibility continues through recovery, recognition of postoperative complications and follow-up. The professional statement of the American College of Surgeons treats postoperative responsibility and continuity as part of surgical care.^[ref] A perioperative pathway therefore crosses professional and organizational boundaries rather than ending when the incision is closed.

Evaluating such a pathway requires defining both the outcome and the population followed. In an illustrative study, suppose 100 people are scheduled, 92 undergo the operation and 80 have a recorded follow-up outcome. If eight of those 80 have a specified postoperative complication, the observed rate among complete records is $8/80=10\%$. Across all 92 operated people, the possible rate ranges from $8/92\approx 8.7\%$ to $20/92\approx 21.7\%$, depending on the 12 missing outcomes. These are invented counts for a denominator example, not observed clinical rates.

The calculation shows why reporting only a recovery percentage can conceal important missing data. A comparison of care pathways also needs comparable case definitions, observation periods and patient characteristics. Measurements of pain, function, complications and use of resources describe different aspects of recovery; combining them into one endpoint changes the question being answered.

Perioperative care is consequently both clinical coordination and a problem of reliable measurement. A useful scientific account states what intervention changed, which stage of care it affected, who was observed and how the resulting clinical outcomes were assessed.

A postoperative complication is an adverse development that deviates from the anticipated course after an operation. Its definition must specify what counts as an event, when it is observed and how it is distinguished from an expected consequence or failure to achieve the operation’s original aim. The primary 2004 classification paper explicitly distinguishes complications, inherent sequelae and failure to cure.^[ref]

The Clavien-Dindo classification provides one systematic way to describe severity, largely using the treatment required and the consequences of the complication. The authors evaluated the revised scheme in a cohort of 6,336 surgical patients and an international survey, addressing both clinical associations and reproducibility of classification.^[ref] A severity grade and the incidence of complications answer different questions: an uncommon severe event and several minor events cannot be summarized faithfully by an unspecified count.

Consider an illustrative series of 40 people with one operation each. Five people experience a total of eight defined complications. The proportion of people with at least one complication is $5/40=12.5\%$, whereas the event count per operation is $8/40=0.20$. Those figures use the same observations but measure different quantities. Counting only the most severe event for each person produces yet another summary.

Follow-up also changes what can be observed. Events after discharge are missed by a study limited to the initial hospital stay, and missing data can distort a comparison. A useful report states the eligible population, observation period, event definitions, severity rules and whether repeated events are included. Comparing surgical outcomes additionally requires accounting for differences in the people and procedures being compared.

An event occurring after an operation does not, by timing alone, establish which part of care caused it. The classification of an outcome, the measurement of its frequency and a causal explanation are separate scientific tasks. Clear definitions make each task more reproducible and connect complication reporting to the wider evaluation of perioperative care.

A statistician develops or applies methods for collecting data and learning from it under uncertainty. The work connects experimental design, probability models, estimation and statistical hypothesis testing. For example, deciding how many independent observations to collect requires linking the desired precision of a confidence interval to the variation expected under a statistical model. Interpreting results also requires examining sampling bias, missing data and assumptions about dependence.