Types of studies

We will include randomised controlled trials (RCTs) and controlled clinical trials that use quasi‐randomised methods to allocate participants to study groups (for example, date of birth or alternate allocation). We will include studies reported as full text, those published as abstract only, and unpublished data. There has been a move towards pragmatic and adaptive trial designs, given the ethical and logistical difficulties with performing placebo‐controlled RCTs in paediatric rheumatic conditions (Balevic 2017). We will include blinded withdrawal trials, with the primary objective of proving drug efficacy, if the study cohort includes youth who achieved a state of clinically inactive disease during the interventional phase of the trial (Amarilyo 2016). However, cross‐over trials are not a suitable study design for this question, so we will exclude them. Cluster‐randomised trials are unlikely to be used to address this question, so we will also exclude them. There will be no language restrictions.

Types of participants

We will include children and young people under 21 years of age, with a diagnosis of juvenile idiopathic arthritis (JIA) and clinically inactive disease. The JIA should have been diagnosed using the International League Against Rheumatism (ILAR) criteria (Petty 2004), or earlier equivalents, including criteria from the European League Against Rheumatism (EULAR (Fantini 1977)), or American College of Rheumatology (ACR (Cassidy 1989)).

Clinically inactive disease should be defined using the Wallace criteria (Wallace 2004; Wallace 2011), the clinical Juvenile Arthritis Disease Activity Score (cJADAS (Consolaro 2014)), or as defined by the study authors.

Systemic onset juvenile idiopathic arthritis (SoJIA) is genetically and pathophysiologically different from other subtypes of JIA, with different long‐term outcomes compared to other subtypes (Guzman 2015; Sengler 2015; Tiller 2018). Given these observations, it has been argued that it should be considered a separate entity (Ramanan 2005). Some contemporary trials and management guidelines differentiate between systemic and non‐systemic JIA (Ringold 2019). Given these differences, we plan on performing two separate reviews: 

• One on SoJIA including all patients with a diagnosis of SoJIA and active systemic disease ; and 

• One on non‐systemic JIA (defined as all youth with JIA without active systemic features; this may include patients with oligoarticular JIA, polyarticular JIA, psoriatic JIA, enthesitis related JIA, undifferentiated JIA and systemic JIA with active arthritis but no active systemic symptoms).

If we identify a trial with only a subset of eligible participants, we will only include it if data specific to the subset of interest are available.

Types of interventions

We will include trials comparing disease‐modifying anti‐rheumatic drug (DMARD) dose reduction or discontinuation with a continuing, static dose of DMARDs (no dose reduction or discontinuation).

The dose reduction or discontinuation strategies to be included in this review are:

• Dose reduction by:

  • Down‐titration to a lower dose (e.g. 40 mg adalimumab once every two weeks, reduced to 20 mg once every two weeks); or

  • Increasing the interval between doses (e.g. 40 mg adalimumab once every two weeks, reduced to 40 mg once every three weeks); or

  • Relative down‐titration, by leaving a fixed dose rather than adjusting for anthropometric changes (e.g. allowing the young person to 'grow out of a dose', by leaving a fixed dose at 10 mg methotrexate once every week, rather than targeting a dose relative to body surface area that will increase throughout childhood).

• Discontinuation (without prior dose reduction)

All disease‐modifying treatments for JIA will be eligible for inclusion. These will include, but not be limited to, the following treatments:

• Conventional synthetic DMARDs (csDMARDs), such as methotrexate, leflunomide, sulfasalazine, and hydroxychloroquine, that do not target a specific molecular structure; or

• Biologic DMARDs (bDMARDs), such as infliximab, etanercept, adalimumab, certolizumab, golimumab, tocilizumab, sarilumab, anakinra, rilonacept, canakinumab, abatacept, and rituximab that are derived biologically, and are designed to target specific cells or proteins involved in the inflammatory response present in JIA. Because these are biologically derived proteins, it is impossible to exactly reproduce their complex structure. Biologic DMARDs can be further classified into bio‐originator and bio‐similar DMARDs, to specify whether they were made by the first or subsequent manufacturers; or

• Targeted synthetic DMARDs (tsDMARDs), such as tofacitinib, baricitinib, and upadacitinib that similarly to bDMARDs, are designed to act on a specific molecular target.

We will include studies in which participants receive various co‐interventions, provided the co‐interventions are applied similarly in all treatment groups.

Types of outcome measures

There are no standardised core set outcome measures for JIA. Contemporary outcome domains have been established, however specific outcome measures for these domains are yet to be determined (Morgan 2019).

We will not exclude studies on the basis of whether outcomes are reported.

Electronic searches

We will base our search methods on a model developed by Cochrane Musculoskeletal for a current living systematic review on rheumatoid arthritis (Hazlewood 2020).

We will conduct an electronic database search in the Cochrane Central Register of Controlled Trials (CENTRAL) Ovid, MEDLINE Ovid, and Embase Ovid, combining standard Cochrane search filters for 'juvenile idiopathic arthritis' and 'randomised trial' (Appendix 1). We will supplement this with a search of the US National Institutes of Health Ongoing Trials Register ClinicalTrials.gov (ClinicalTrials.gov) and the World Health Organization International Clinical Trials Registry Platform (ICTRP; www.who.int/ictrp/en), using the search term 'juvenile idiopathic arthritis'.

We intentionally designed our search to not include terms for the intervention. This allows us to establish a record of all randomised trials in this condition, regardless of the intervention. Our hope is that this could be used to facilitate future efficient reviews of interventions other than the ones considered under our eligibility criteria. While our broad search will expand the volume of records, we will consider using project enhancements (e.g. Cochrane Crowd) to facilitate the screening process (Cochrane Crowd 2019).

We will search all databases from their inception to the present, and we will impose no restriction on language of publication.

Searching other resources

We will check reference lists of all included primary studies and identified review articles for additional references.

Selection of studies

We will initially screen the records using an approach that combines machine learning and crowdsourcing to identify probable RCTs. First, we will upload the search results to a RCT classifier, available in the Cochrane Register of Studies (CRS‐Web (Wallace 2017)). The classifier uses machine learning algorithms to assign a probability of each citation being a true RCT. We will assume citations with a < 1% probability of being a RCT to be non‐RCTs, and exclude them. If the yield is too large for the review team to screen, we will upload the remaining records to Cochrane Crowd, a citizen science platform, launched in 2016. Cochrane Crowd uses a crowdsourcing approach to conduct small discrete tasks, which help identify and describe health research in different areas. Reviewers are categorised as novices, experts (individuals who screened > 1000 abstracts and had at least 95% recall and specificity to a reference standard), and resolvers (individuals who are used to settle any disagreements or uncertainties in judgements). If only novices are involved, three consecutive, consistent judgements are required to move a study to the next stage. If at least one screener is an expert, then only two consecutive agreements are required. Any designation of unsure sends an abstract to a resolver, as do any disagreements.

Any citations that are deemed to be potential RCTs by Cochrane Crowd will be returned to the review authors for screening. This hybrid machine learning/crowdsourcing approach has been validated in a study that demonstrated a specificity of 99.8% and an overall recall of 98% when identifying RCTs (Wallace 2017).

Data extraction and management

We will use a standard data collection form to extract study characteristics and outcome data. We will pilot the form on at least one study in the review. At least two review authors (WR, JT, JA, RJ) will independently extract study characteristics from included studies onto a separate Excel spreadsheet. A third review author (JM) will review the study extraction documentation completed by the original two review authors (WR, JT, JA, RJ) against the published clinical trial report or unpublished manuscript to confirm veracity of the data. We will extract the following study characteristics:

1. Methods: study design, total duration of study, details of any treatment 'run‐in' period, number of study centres and location, study setting, withdrawals, and date of study

2. Participants: N, mean age, age range, sex, disease duration, JIA subtype, diagnostic criteria used, duration of inactive disease or remission, joint count, C‐reactive protein (CRP), erythrocyte sedimentation rate (ESR), degree of uveitis activity (using SUN criteria for anterior chamber (AC) flare and grading for AC cells (Jabs 2005)), presence of systemic symptoms (fever, rash, serositis, splenomegaly, lymphadenopathy attributable to JIA), cJADAS score, the CHAQ (Childhood Health Assessment Questionnaire) as a functional/participation outcome, physician global assessment of disease activity score (Filocamo 2010), patient/parent global assessment of disease activity score (Filocamo 2010), episodes of macrophage activation syndrome (Ravelli 2016), trial inclusion criteria, and trial exclusion criteria

3. Interventions: name of drug, dose, mode of administration (i.e. oral, or subcutaneous in the case of methotrexate), treatment duration, intervention category (fixed dose reduction, disease activity‐guided dose reduction, therapeutic drug monitoring‐guided dose reduction, or discontinuation without prior dose reduction) and description of dose reduction strategy used (e.g. reduction in dose and time frame at reduced dose, or widening of interval between doses, or abrupt cessation of agent without prior dose reduction); co‐intervention (name of drug, dose, duration, and frequency of co‐intervention treatment); permitted concomitant medications, including stable doses of certain analgesics, non‐steroidal anti‐inflammatory drugs (NSAIDs), and DMARDs

4. Comparisons: name of drugs; dose, treatment duration, treatment frequency or intervals; co‐intervention (name of drugs, dose, duration, and frequency of co‐intervention treatment); permitted concomitant medications

5. Outcomes: primary and secondary outcomes specified and collected, and time points reported

6. Characteristics of the design of the trial, outlined below in the 'Assessment of risk of bias in included studies' section

7. Notes: funding for trial, and notable declarations of interest of trial authors; details of any correspondence with study authors

At least two review authors (WR, JT, JA, RJ) will independently extract outcome data from included studies. We will extract the number of events and number of participants per treatment group for dichotomous outcomes, and means and standard deviations and number of participants per treatment group for continuous outcomes. We will note in the 'Characteristics of included studies' table if outcome data were not reported in a usable way, and when data were transformed or estimated from a graph. We will resolve disagreements by consensus, or by involving a third person (JM). One review author (WR, JT, JA, RJ) will transfer data into the Review Manager 5 file (Review Manager 2020). We will double‐check that data are entered correctly by comparing the data presented in the systematic review with the study reports.

We will use PlotDigitizer to extract data from graphs or figures if means and measures of variance are not reported in the text of included studies (PlotDigitizer 2020) to extract data from graphs or figures if means and measures of variance are not reported in the text of included studies. We will also extract these data in duplicate.

As these diseases have heterogeneous presentations, monitoring often includes a broad variety of assessments. If more than one measure is used for an outcome, we will use the following prespecified hierarchy for definition of remission:

• Proportion of participants with clinical remission (Wallace criteria)

• Proportion of participants with clinically inactive disease (cJADAS score)

We will apply these decision rules in the event of multiple outcome reporting:

• If both final values and change from baseline values are reported for the same outcome, we will extract final values

• If both unadjusted and adjusted values are reported for the same outcome, we will extract adjusted values

• If data are analysed based on an intention to treat (ITT) sample and another sample (e.g. per‐protocol, as‐treated), we will extract ITT data

• If multiple time points are reported, we will extract the data at the time point of longest duration

Assessment of risk of bias in included studies

At least two review authors (WR, JT, JA, RJ) will independently assess risk of bias for each study using the criteria outlined in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2017). We will resolve any disagreements by discussion, or by involving another author (JM).

We will assess the risk of bias according to the following domains:

• Random sequence generation

• Allocation concealment

• Blinding of participants and personnel

• Blinding of outcome assessment

• Incomplete outcome data

• Selective outcome reporting

• Other bias, such as unequal application of co‐interventions

We are primarily interesting in assessing the effect of assignment to the interventions at baseline, regardless of whether the interventions are received as intended (intention to treat).

We will grade each potential source of bias as high, low, or unclear risk, and provide a quote from the study report together with a justification for our judgment in the risk of bias table. We will summarise the risk of bias judgements across different studies for each of the domains listed. We will consider blinding separately for different key outcomes when necessary (e.g. for unblinded outcome assessment, risk of bias for proportion of participants with sustained clinically inactive disease may be different than for serious adverse events). As well, we will consider the impact of missing data by key outcomes.

When information on risk of bias relates to unpublished data or correspondence with a trialist, we will note this in the risk of bias table.

When considering treatment effects, we will take into account the risk of bias for the studies that contribute to that outcome.

We will present the graphs generated by the risk of bias (RoB 1) tool to provide summary assessments of the risk of bias.

Measures of treatment effect

We will analyse dichotomous data as risk ratios (RR), or Peto odds ratios (OR) when the outcome is a rare event (approximately less than 10%), and use 95% confidence intervals (CIs). We will analyse continuous data as mean differences (MD) or standardised mean differences (SMD), depending on whether the same scale is used to measure an outcome, and 95% CIs. We will enter data presented as a scale with a consistent direction of effect across studies.

When different scales are used to measure the same conceptual outcome (e.g. disability), we will calculate SMDs with corresponding 95% CIs. We will back‐translate SMDs to a known scale (e.g. 0 to 10 for pain) by multiplying the SMD by a typical among‐person standard deviation (e.g. the standard deviation of the control group at baseline from the most representative trial (Higgins 2019)). We will analyse time‐to‐event data as hazard ratios (HR). We will use Poisson methods to analyse rate data.

For dichotomous outcomes, we will calculate the number needed to treat for an additional beneficial outcome (NNTB), or the number needed to treat for an additional harmful outcome (NNTH) from the control group event rate and the relative risk, using the Visual Rx NNT calculator (Cates 2008). For continuous measures, we will calculate the NNTB or NNTH using the Wells calculator (available at the CMSG Editorial office; musculoskeletal.cochrane.org/). We will use the minimal clinically important difference (MCID) in the calculation of NNTB or NNTH.

The MCID has not formally been defined or validated for the cJADAS, however, an MCID of +1.7 has been determined for worsening on the JADAS‐27 (a similar scale, which also includes a normalised ESR value in calculating an overall score (Bulatović Ćalasan 2014)). For the purpose of this study, we will use an MCID of +1.7 on the cJADAS for worsening, because the addition of ESR is unlikely to have a clinically meaningful effect in a cohort of youth with clinically inactive disease at baseline. We will use an MCID of 10% for other measures, including the proportion of participants with sustained remission.

For dichotomous outcomes, we will calculate the absolute per cent change from the difference in the risks between the intervention and control group, using GRADEpro GDT software, expressed as a percentage (GRADEpro GDT). We will calculate the relative per cent change as the risk ratio ‐ 1, expressed as a percentage.

For continuous outcomes, we will calculate the absolute per cent change by dividing the mean difference by the scale of the measure, expressed as a percentage. We will calculate the relative difference as the absolute benefit (mean difference) divided by the baseline mean of the control group, expressed as a percentage.

In the 'Effects of interventions' results section and the 'What happens' column of the summary of findings table, we will provide the absolute per cent change, the relative per cent change from baseline, and the NNTB or NNTH (we will provide the NNTB or NNTH only when the outcome shows a clinically significant difference).

Unit of analysis issues

For trials with more than two arms, we will describe all study groups in the ’Characteristics of included studies’ table, but we will only include the intervention groups that meet our review criteria in the analysis. When the variance of the difference between intervention and comparator is not reported, we will calculate this from the variances of all trial arms. When a study includes multiple relevant treatment arms, we will combine groups to perform a single pairwise comparison (Higgins 2019). If this prevents identification of potential heterogeneity, we will analyse each group separately, against a common control group. However, to ensure that a common control group is not included multiple times in a meta‐analysis that includes several interventions from the same trial, we will proportionately reduce control group data. For example, in a study with two interventions and a single control group, we will halve the numbers of participants and events in the control group. When studies report only differences between treatment groups, as opposed to mean effects for each group, we will analyse data using the generic inverse variance function.

Dealing with missing data

We will contact investigators or study sponsors in order to verify key study characteristics and obtain missing numerical outcome data, when possible (e.g. when a study is identified as abstract only). When possible, we will use the Review Manager 5 calculator to calculate missing standard deviations, using other data from the trial, such as confidence intervals, based on methods outlined in the Cochrane Handbook (Higgins 2019). When this is not possible, and the missing data are thought to introduce serious bias, we will explore the impact of including such studies in the overall assessment of results with a sensitivity analysis.

For dichotomous outcomes (e.g. number of withdrawals due to adverse events), we will calculate the withdrawal rate using the number of participants randomised to the group as the denominator. For continuous outcomes (e.g. mean change in pain score), we will calculate the MD or SMD based on the number of participants analysed at that time point. If the number of participants analysed is not presented for each time point, we will use the number of randomised participants to each group at baseline.

Assessment of heterogeneity

We will assess clinical and methodological diversity of participants, interventions, outcomes, and study characteristics of the included studies to determine whether a meta‐analysis is appropriate. We will inspect forest plots visually to consider the direction and magnitude of effects, and the degree of overlap between confidence intervals. We will use the I² statistic to quantify inconsistency among the trials in each analysis. We will also consider the P value from the Chi² test.

As recommended in the Cochrane Handbook for Systematic Reviews of Interventions, the interpretation of an I² value of 0% to 40% might not be important; 30% to 60% may represent moderate heterogeneity; 50% to 90% may represent substantial heterogeneity; and 75% to 100% may represent considerable heterogeneity (Deeks 2019). We will keep in mind that the importance of I² depends on the: (i) magnitude and direction of effects, and (ii) strength of evidence for heterogeneity.

We will interpret the Chi² test as indicating evidence of statistical heterogeneity when P ≤ 0.10.

If we identify substantial heterogeneity, we will report it, and investigate possible causes by following the recommendations in Chapter 10 of the Cochrane Handbook (Deeks 2019).

Assessment of reporting biases

If we are able to pool more than 10 trials, we will create and examine a funnel plot to explore possible small study biases for the major outcomes. In interpreting funnel plots, we will examine the possible reasons for funnel plot asymmetry, as outlined in Chapter 13 of the Cochrane Handbook for Systematic Reviews of Interventions, and relate this to the results of the review (Page 2020).

To assess outcome reporting bias, we will check trial protocols against published reports. For studies published after 1 July 2005, we will screen the trial registries for the a priori trial protocol. We will evaluate whether selective reporting of outcomes is present.

Data synthesis

The primary analysis will include all studies, independent of the risk of bias assessments. We will present two main comparisons: (i) dose reduction compared with continuation; and (ii) abrupt discontinuation (without prior dose reduction) compared with continuation to provide estimates of benefit and harm. We plan to synthesise effect estimates using a random‐effects model, based on the assumption that clinical diversity is likely to exist, and different studies are estimating different intervention effects.

When we cannot pool data, we will present effect estimates and 95% CIs of each trial in tables, and summarise the results in the text.

Subgroup analysis and investigation of heterogeneity

For the non‐systemic JIA review, we plan to carry out the following subgroup analysis, to assess if there are potential differences in sustained clinically inactive disease by JIA subtype. For each of the JIA subtypes (oligoarthritis, polyarthritis (rheumatoid factor negative), polyarthritis (rheumatoid factor positive), psoriatic arthritis, enthesitis related arthritis, undifferentiated arthritis), we will measure the proportion of each subgroup that sustains clinically inactive disease, following reduction or discontinuation of their medication.

We do not plan on performing a subgroup analysis for the SoJIA review.

We will use the formal test for subgroup interactions in Review Manager 5, and will use caution in the interpretation of subgroup analyses, as advised in Chapter 10 of the Cochrane Handbook (Deeks 2019; Review Manager 2020).

Sensitivity analysis

We plan to carry out the following sensitivity analyses to investigate the robustness of the treatment effect (proportion of participants sustaining clinical inactive disease) to potential selection and detection biases:

1. Selection bias: we will remove the trials that reported inadequate or unclear allocation concealment from the meta‐analysis, to see if this changes the overall treatment effect.

2. Detection bias: we will remove the trials that reported inadequate or unclear participant blinding from the meta‐analysis, to see if this changes the overall treatment effect.

3. Impact of missing data: we will remove studies with imputed data to see if there is an effect.

Summary of findings and assessment of the certainty of the evidence

We will use methods and recommendations described in Chapter 14 of the Cochrane Handbook for Systematic Reviews of Interventions, and GRADEpro GDT software to develop and display the summary of findings tables (GRADEpro GDT; Schünemann 2019a). We will justify all decisions to downgrade the certainty of the evidence using footnotes, and we will make comments to aid reader's understanding of the review, where necessary.

We will provide the number needed to treat for an additional beneficial outcome (NNTB) or the number needed to treat for an additional harmful outcome (NNTH), and the absolute and relative per cent change in the comments column of the summary of findings tables, as described in the 'Measures of treatment effect' section.

At least two review authors (WR, JT, JA, RJ) will independently assess the certainty of the evidence. We will use the five GRADE considerations (study limitations, consistency of effect, imprecision, indirectness, and publication bias) to assess the certainty of a body of evidence as it relates to the studies that contributed data to the meta‐analyses for the prespecified outcomes, and report the certainty of the evidence as high, moderate, low, or very low.

The first summary of findings table will compare:

• Dose reduction (without discontinuation) of systemic therapies compared with continuation of systemic therapies

The second summary of findings table will compare:

• Abrupt discontinuation (without prior dose reduction) of systemic therapies compared with continuation of systemic therapies

We will include the following outcomes in each table:

• Proportion of participants with sustained clinically inactive disease

• Proportion of participants with sustained remission off medication

• Proportion of participants with flare of articular disease

• Proportion of participants with flare of ocular disease

• Proportion of participants with flare of systemic disease

• Serious adverse events

• Study withdrawal due to adverse events

We will use the primary time point (over three months and up to six months) for the primary comparison in each summary of findings table.