Tipos de estudios

Esta revisión incluyó ECA independientemente del estado de publicación. No se aplicaron restricciones de idioma.

Tipos de participantes

Los participantes incluyeron a pacientes (≥ 16 años de edad) con EC activa que se diagnosticó mediante una evaluación clínica, endoscópica, radiográfica e histopatológica estándar. La EC activa se definió como una puntuación del Crohn’s Disease Activity Index (CDAI) superior a 150 o una puntuación del Harvey‐Bradshaw Index (HBI) superior a 4 (Best 1976; Harvey 1980).

Tipos de intervenciones

La administración subcutánea de cualquier dosis de CZP cada dos a cuatro semanas en comparación con placebo o ningún tratamiento. Los comparadores activos como el tratamiento convencional (incluido el ácido 5‐aminosalicílico, los inmunomoduladores o los corticosteroides) no se incluyeron en esta revisión.

Tipos de medida de resultado

Búsquedas electrónicas

We conducted a comprehensive literature search without language restrictions. We searched the following databases to identify relevant RCTs:

• MEDLINE (inception to date);

• Embase (inception to date);

• CENTRAL;

• The Cochrane IBD Group Specialized Register (inception to date);

• http://ClinicalTrials.gov (trial registry);

• https://www.clinicaltrialsregister.eu/ (EU Clinical Trials Register);

• http://apps.who.int/trialsearch/ (International Clinical Trials Registry Platform); and

• http://www.ucb.com/our‐science/Our‐clinical‐studies/cimzia‐certolizumab‐pegol (web site of a pharmaceutical company producing CZP).

The search strategies are reported in Appendix 1.

Búsqueda de otros recursos

To identify additional studies, we searched the following resources manually or through personal contacts:

• Abstracts of Digestive Disease Week, United European Gastroenterology Week, European Crohn’s and Colitis Organization Congress, and Advances in Inflammatory Bowel Diseases (2000 to date);

• References from published articles; and

• Pharmaceutical companies and experts involved in the development of CZP.

Selección de los estudios

Two authors (HY and RS) independently screened titles and abstracts, and selected potential eligible studies based on the above criteria. In addition, these authors independently read the full‐text articles of the potential eligible studies and decided which studies should be included in the review. In cases of insufficient information, we contacted the authors of the primary studies to evaluate eligibility for inclusion. In the event of a disagreement regarding study selection, HY and RS discussed the matter together to reach a consensus. NW acted as the arbitrator when consensus was not reached.

Extracción y manejo de los datos

Two authors (HY and RS) independently extracted data using data extraction forms to record data from the selected studies. Any disagreements were resolved through discussion. NW was the arbitrator when consensus was not reached.

We extracted the following data:

• Characteristics of the primary studies: publication year, country, study recruitment period, study completion date, study type, and risk of bias items;

• Participant characteristics: country, total number of participants, number of participants randomized, number of participants analyzed in each group, age, sex, ethnicity, body mass index, disease duration, disease site, smoking status, CDAI score, HBI score, CDEIS, SES‐CD, Rutgeerts score, IBDQ score, SF‐36 score, CRP, fistula, concurrent CD treatment, previous CD treatment, inclusion criteria, and exclusion criteria;

• Intervention characteristics: dose, delivery route, and administration schedule of CZP;

• Comparator characteristics: placebo or no treatment control;

• Outcomes: proportion of participants who achieved clinical remission at week 8, proportion of participants with clinical response at week 8, CDAI score at week 8, HBI score at week 8, CDEIS at week 12, SES‐CD at week 12, Rutgeerts score at week 12, IBDQ score at week 8, SF‐36 score at week 8, CRP at week 8, fistula closure at week 8, any adverse events, adverse events leading to withdrawal, serious adverse events, time of outcome assessment in primary studies, length of follow‐up, number of participants lost to follow‐up, reasons for loss to follow‐up, number of participants who did not complete treatment, reasons for incomplete treatment, and criteria for evaluating outcomes in primary studies.

We contacted the authors of the primary studies and the pharmaceutical company that manufactures CZP if information in the published reports was insufficient.

Evaluación del riesgo de sesgo de los estudios incluidos

Two authors (HY and RS) independently assessed the quality of included studies using the Cochrane risk of bias tool (Higgins 2011). Any disagreements were resolved by consensus with a third author (NW). Primary studies were rated as high, low, or unclear risk of bias. We assessed the following risk of bias items: random sequence generation (selection bias), allocation concealment (selection bias), blinding of participants and personnel (performance bias), blinding of outcome assessment (detection bias), incomplete outcome data (attrition bias), selective reporting (reporting bias), and other potential sources of bias.

We rated random sequence generation as low risk of bias if the method for random sequence generation was described as a random number table, computer‐generated, coin tossing, shuffling cards or envelopes, throwing dice, drawing of lots or minimization. We rated random sequence generation as high risk of bias if the method of generation was not random. Examples included a systematic approach, such as date or record number, or a non‐systematic approach, such as preference and availability. We rated random sequence generation as unclear risk of bias if insufficient information was reported to allow for a judgement.

We rated allocation concealment as low risk of bias if allocation could not be foreseen by participants and investigators. Adequate methods of allocation concealment included centralized allocation such as telephone, web‐based, or pharmacy‐controlled randomization, sequentially numbered drug containers of the same appearance, or sequentially numbered, opaque, sealed envelopes. We rated allocation concealment as high risk of bias if the allocation sequence was likely to be foreseen. Examples included an open random allocation schedule or envelopes without safeguards. We rated allocation concealment as unclear risk of bias if insufficient information was reported to allow for a judgement.

We rated blinding of participants and personnel and blinding of outcome assessors as low risk of bias if proper methods were employed to prevent knowledge of treatment assignment (e.g. double‐blinding with an identical placebo) or if no blinding or incomplete blinding of participants or personnel was unlikely to affect assessment of the outcome (e.g. a serious adverse event resulting in death). We rated blinding of participants and personnel and blinding of outcomes assessors as high risk of bias if blinding was likely to be broken and this could affect outcome assessment, or if there was no blinding or incomplete blinding of participants or personnel or outcome assessors which could affect outcome assessment. We rated blinding of participants and personnel and blinding of outcome assessors as unclear risk of bias if insufficient information was reported to allow for a judgement.

We rated incomplete outcome data as low risk of bias when there were no missing outcome data; when missing outcome data were unlikely to be related to the true outcome; when the number of dropouts and reasons for withdrawal were balanced between treatment groups; when compared to the observed event, the proportion of missing outcomes did not have a clinically relevant impact on the effect estimate for dichotomous outcomes; when the expected effect size among missing outcomes did not have clinically relevant impact on the observed effect size for continuous outcome data; or when missing data were imputed using proper methods. We rated incomplete outcome data as high risk of bias when missing outcome data were likely to be related to the true outcome; when numbers or reasons for missing data were imbalanced across treatment groups; when compared with the observed event, the proportion of missing outcomes had a clinically relevant impact on the effect estimate for dichotomous outcomes; when the expected effect size among missing outcomes had a clinically relevant impact on the observed effect size for continuous outcomes; when an 'as‐treated analysis' was substantially performed; and when missing data were imputed using improper methods (e.g. simple imputation). We rated incomplete outcome data as unclear risk of bias when insufficient information was reported to allow for a judgement.

We rated selective reporting as low risk of bias when the protocols of primary studies were available, and all of the primary and secondary study outcomes related to this systematic review, were reported in a pre‐defined way; and when the study protocols were unavailable, but all of the expected outcomes, related to this systematic review, were reported. We rated selective outcome reporting as high risk of bias when pre‐defined primary outcomes related to this systematic review were not thoroughly reported; when those primary outcomes were measured or analyzed in a way that was different to the protocol; when reported primary outcomes related to this systematic review were different from those in the protocol; when the outcomes were not completely reported; and when key outcomes were not included in the primary studies. We rated selective outcome reporting as unclear risk of bias when insufficient information was reported to allow for a judgement.

We rated studies as low risk of bias for other sources of bias when the study appeared to be free of other potential sources of bias. We rated studies as high risk of bias for other sources of bias when other sources of bias could have an impact on the study outcomes. For example, fraudulent studies or baseline imbalances in demographic factors. We rated studies as unclear risk of bias for other sources of bias when the study reported insufficient details to allow for a judgement. We contacted study authors for additional information to clarify the risk of bias when the study reports did not provide enough detail to allow for a clear judgement.

Medidas del efecto del tratamiento

For dichotomous outcomes, we calculated the risk ratio (RR) and corresponding 95% confidence interval (CI). ITT analyses were conducted for dichotomous outcomes, whereby all dropouts were assumed to be treatment failures. We calculated the mean difference (MD) and 95% CI for continuous outcomes. When different scales were used to measure the same construct, we planned to calculate the standardized mean difference (SMD) and 95% CI.

Cuestiones relativas a la unidad de análisis

We collected outcomes per randomized participant. For cross‐over trials, we planned to use data from the first phase before the cross‐over. Cluster RCTs were not included in this review. If events occurred more than once (e.g. adverse events), we reported on the proportion of participants who experienced at least one event. To avoid double counting of the comparator for multi‐arm studies (multiple dose groups), the number of patients in the comparator group (i.e. placebo or no treatment control) were divided across the number of eligible CZP arms. To deal with multiple observations for the same outcome in primary studies, we precisely defined the outcome assessment points for both primary and secondary outcomes.

Manejo de los datos faltantes

We contacted authors of the primary studies and the pharmaceutical company that manufactures CZP to obtain missing data and the reason for missing data. If it was not possible to obtain the missing data, we reported as such in the results. For dichotomous outcomes, all missing data were treated as treatment failures in the ITT analyses. We conducted sensitivity analyses using available case data to assess the impact on the effect estimate. For continuous outcomes, we did not use any imputation methods, and used the available data only.

Evaluación de la heterogeneidad

Clinical heterogeneity was first assessed with regard to patient characteristics, such as previous treatment and concurrent medication. If the studies were clinically homogenous, statistical heterogeneity was evaluated using the Chi² test and I² statistic. A P value of less than or equal to 0.10 for the Chi² test was considered to show statistically significant heterogeneity. The I² statistic estimates the degree of statistical heterogeneity. We considered an I² value of 25% to indicate low heterogeneity, a value of 50% to indicate moderate heterogeneity and a value of 75% to indicate high heterogeneity. If statistical heterogeneity existed, we planned to perform a visual inspection of the forest plots to identify potential outliers causing the heterogeneity. Moreover, sensitivity and subgroup analyses were planned to explore potential sources of heterogeneity when significant or moderate‐high heterogeneity was identified (Higgins 2003; Higgins 2011).

Evaluación de los sesgos de notificación

We searched for both registered and published trials, and reported on the proportion of registered trials that were unpublished. We contacted the investigators of the unpublished trials and the pharmaceutical company that manufactures CZP to provide data related to outcomes in this systematic review. If we could not obtain these data, we reported as such in this review. When there were 10 or more eligible trials in a pooled analysis, we planned to generate funnel plots to evaluate potential publication bias. Moreover, when we found unclear or high risk of bias for selective reporting, we contacted the study authors and the pharmaceutical company that manufactures CZP to provide unpublished outcome data. If we could not obtain these data, we reported so in the results.

Síntesis de los datos

When included studies were sufficiently similar from the clinical and statistical viewpoints, we conducted meta‐analyses. Data were analyzed using Review Manager 5.3, and a random‐effects model was used for the meta‐analyses. A P value of less than 0.05 was considered to be statistically significant.

On the basis of the characteristics of participants, interventions, and outcomes in primary studies, clinical similarity was determined by consensus between HY and KM. In cases of disagreement between HY and KM, the authors consulted with TK to resolve the disagreement. In cases of high heterogeneity (I² statistic ≥ 75%), meta‐analyses were not planned, and each study was planned to be described in detail.

Análisis de subgrupos e investigación de la heterogeneidad

If sufficient data were available, the following subgroup analyses were planned for the primary outcomes:

• Disease severity at baseline (150 < CDAI < 220, 220 ≤ CDAI ≤ 450, CDAI > 450);

• CRP levels at baseline (CRP levels < 10 mg/L, CRP levels ≥ 10 mg/L);

• Doses of CZP (CZP < 200 mg, 200 mg ≤ CZP < 400 mg, 400 mg ≤ CZP < 600 mg, and CZP ≥ 600 mg); and

• Previous treatment with other TNF‐α inhibitors (yes, no).

Análisis de sensibilidad

We planned to perform the following sensitivity analyses for primary outcomes:

• Excluding studies judged to be at high risk of bias for any domain of the risk of bias tool;

• Excluding studies judged to be at high or unclear risk of bias for any domain of the risk of bias tool;

• Using available case data instead of ITT analysis for missing dichotomous outcome data;

• Selecting later outcome assessment points if only dates from two time points equally distant from the defined outcome assessment points were available despite inquiring with the original investigators. For example, if only dates from two time points equally distant from week 8, such as weeks 6 and 10, were available, week 10 was planned to be selected in the sensitivity analysis.

• Limiting the included studies that administered CZP strictly in accordance with the approved regimen which is subcutaneous administration of 400 mg CZP at weeks 0, 2, and 4, and then every 4 weeks.