Types of studies

We included all published, unpublished, and ongoing randomised controlled trials (RCTs) and quasi‐RCTs (RCTs in which treatment allocation was determined by alternation, use of alternate medical records, date of birth, or other predictable methods).

Types of participants

Participants of any age with CKD stages 3–5D as defined by the K/DOQI (Levey 2003) or the KDIGO guidelines (Eknoyan 2013) were considered for inclusion. The review excluded patients who had a functioning kidney transplant or were those treated with corticosteroids, because corticosteroids strongly contribute to the progression of osteoporosis. Additionally, two Cochrane reviews have already evaluated these populations (Allen 2016; Palmer 2019). The target population included patients with evidence of severe osteopenia or osteoporosis according to WHO criteria (T score < −2.0 SD). The International Society for Clinical Densitometry suggests that the diagnosis of osteoporosis in children and adolescents should not be made based on densitometric criteria alone (ISCD 2019). Thus, based on a previous study (Ward 2007), children who had at least one low‐trauma fracture and/or reduced BMD were included.

Types of interventions

Patients receiving anti‐osteoporotic drugs were compared with individuals receiving a placebo, no treatment, or usual care. The primary intervention was treatment with anti‐osteoporotic drugs, including the following:

1. Bisphosphonates (etidronate, clodronate, tiludronate, alendronate, risedronate, ibandronate, pamidronate, zoledronate)

2. Denosumab

3. SERMs (bazedoxifene, raloxifene)

4. Teriparatide

5. Abaloparatide

6. Romosozumab

7. Strontium ranelate

Other treatments (e.g., vitamin D, phosphate binders, calcium supplements, calcimimetics, dialysate calcium adjustment, and dietary calcium or phosphate manipulation) were excluded from primary comparisons but were listed as co‐interventions. This approach was used as these interventions were included in three previous Cochrane reviews (Palmer 2007b; Palmer 2009; Ruospo 2018). We did not place any restrictions on the doses of therapy. All studies had a follow‐up period of at least six months.

Types of outcome measures

Electronic searches

We searched the Cochrane Kidney and Transplant Register of Studies up to 25 January 2021 through contact with the Information Specialist using search terms relevant to this review. The Register contains studies identified from the following sources:

1. Monthly searches of CENTRAL

2. Weekly searches of MEDLINE OVID SP

3. Handsearching of kidney‐related journals and the proceedings of major kidney conferences

4. Searching of the current year of EMBASE OVID SP

5. Weekly current awareness alerts for selected kidney and transplant journals

6. Searches of the International Clinical Trials Register (ICTRP) Search Portal and ClinicalTrials.gov.

Studies contained in the Register were identified through searches of CENTRAL, MEDLINE, and EMBASE based on the scope of Cochrane Kidney and Transplant. Details of search strategies, as well as a list of handsearched journals, conference proceedings and current awareness alerts, are available on the Cochrane Kidney and Transplant website under CKT Register of Studies.

See Appendix 1 for search terms used in strategies for this review.

Searching other resources

1. Reference lists of review articles, relevant studies, and clinical practice guidelines

2. Experts/organisations in the field seeking information about unpublished or incomplete studies

3. Grey literature sources (e.g., abstracts, dissertations, and theses), in addition to those already included in the Cochrane Kidney and Transplant Register of Studies

Selection of studies

Two review authors independently screened the titles and abstracts from search results and coded them as ‘retrieve’ (eligible or potentially eligible/unclear) or ‘do not retrieve’. We retrieved the full text of study reports or publications, which were then independently assessed by two review authors for inclusion. The reason for excluding ineligible studies was recorded. We resolved any disagreement through discussion or, if required, by consultation with a third author. We identified and excluded duplicates studies and collated multiple reports of the same study; this enabled each study rather than each report, to act as a unit of interest in the review. The selection process was recorded in sufficient detail to the enable completion of the PRISMA flow diagram and to generate a table detailing the ‘Characteristics of excluded studies’ (Moher 2009).

Data extraction and management

A data collection form for was used to document study characteristics and outcome data; this form was piloted on at least one study included in the review. The data extraction form included the following items.

• Methods: study design, total duration of study, number of study centres and location, study setting, withdrawals, and date of study

• Participants: number (N), mean age, age range, sex, baseline CKD stage, diagnostic criteria, follow‐up duration, inclusion criteria, and exclusion criteria

• Interventions: intervention, comparison, concomitant medications, and intervention dosage

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

• Notes: funding for studies and notable conflicts of interest reported by study authors, and any other necessary information

Two review authors independently extracted outcome data from the included studies. In the ‘Characteristics of included studies’, we noted if the study authors did not report outcome data in a usable way. We resolved disagreements by consensus or by involving a third author. One review author transferred data into Review Manager. Double data entry was used to confirm that the data were entered correctly data were entered correctly. A second review author spot‐checked study characteristics for accuracy against study reports.

Assessment of risk of bias in included studies

The following items were independently assessed by two authors using the risk of bias assessment tool (Higgins 2011) (see Appendix 2).

• Was there adequate sequence generation (selection bias)?

• Was allocation adequately concealed (selection bias)?

• Was knowledge of the allocated interventions adequately prevented during the study?

  • Participants and personnel (performance bias)

  • Outcome assessors (detection bias)

• Were incomplete outcome data adequately addressed (attrition bias)?

• Were reports of the study free of suggestion of selective outcome reporting (reporting bias)?

• Was the study apparently free of other problems that could put it at a risk of bias?

We judged each potential source of bias as high, low, or unclear, and included text from the study report and justification for our judgement in the risk of bias table. We summarised the risk of bias judgements across studies for each of the domains listed. Blinding was considered for different key outcomes where necessary (e.g., for unblinded outcome assessment, the risk of bias for death (any cause) may be differ from that for a participant‐reported health‐related QoL scale). We contacted study authors for additional information to clarify any risk of bias when the study reports did not provide enough detail to allow for a clear judgement. We considered the risk of bias for studies that contribute to a particular outcome when considering treatment effects.

We assessed the overall risk of bias based on the following bias domains: allocation concealment, blinding of outcome assessors, and incomplete outcome data.

• Low risk of bias: all the above domains are at a low risk of bias

• High risk of bias: one or more of the above domains are at a high or unclear risk of bias

Measures of treatment effect

We analysed dichotomous outcomes as risk ratio (RR) with 95% confidence intervals (CI). Where continuous scales of measurement were used to assess the effects of treatment, the mean difference (MD) or the standardised mean difference (SMD) were used if different scales were used. For outcomes provided as rates, the results were expressed as rate ratios with 95% CIs. If studies included a mixture of change‐from‐baseline and final value scores, we used the (unstandardised) MD method in RevMan according to Chapter 9.4.5.2 of the Cochrane handbook (Higgins 2011). However, the change‐from‐baseline and final value scores were not combined as the SMD, as the SD would reflect the differences in the reliability of the measurements rather than the differences in the measurement scale (Higgins 2011). If a study reported outcomes at multiple time points, we used the last time point recorded. We performed meta‐analyses only when this approach was meaningful; that is, if treatments, participants, and the underlying clinical questions were sufficiently similar to allow for pooling. Skewed data were to be presented descriptively (for example, as medians and interquartile ranges for each group).

Unit of analysis issues

We did not anticipate the inclusion of studies with non‐standard designs, such as cross‐over studies and cluster‐RCTs, in the review. However, studies with multiple arms could be identified and included. In such cases, all intervention groups that were relevant to the review were included. To avoid double counting of the comparator, the number of patients in the comparator group was divided across the number of eligible intervention arms.

Dealing with missing data

Any further information required from the original author was requested in writing by (e.g. emailing the corresponding author), and any relevant information obtained in this manner was included in the review. Important numerical data, such as the number of screened and randomised patients, as well as the intention‐to‐treat (ITT), as‐treated, and per‐protocol populations, were carefully evaluated. Attrition rates, including dropouts, losses to follow‐up, and withdrawals were investigated. Issues of missing data and imputation methods (for example, last‐observation‐carried‐forward) were critically appraised (Higgins 2011).

Assessment of heterogeneity

Heterogeneity was initially assessed by the visual inspection of the forest plots. Thereafter, statistical heterogeneity was quantified using the I² statistic, which described the percentage of total variation across studies that was due to heterogeneity rather than sampling error (Higgins 2003). I² values can be interpreted as follows:

• 0% to 40%: might not be important

• 30% to 60%: may represent moderate heterogeneity

• 50% to 90%: may represent substantial heterogeneity

• 75% to 100%: considerable heterogeneity.

The importance of the observed I² value depended on the magnitude and direction of treatment effects and the strength of evidence for heterogeneity (e.g. P‐value from the Chi² test, or a CI for I²) (Higgins 2011).

Assessment of reporting biases

If possible, funnel plots were used to assess for the potential existence of small study bias (Higgins 2011).

Data synthesis

Different CKD patient populations (patients with CKD stage 3‐5, and patients undergoing dialysis (5D)) were analysed separately. When the selected relevant studies were sufficiently similar, a meta‐analysis was performed. Considering substantial heterogeneity between studies, we used the random‐effects model. If substantial or considerable heterogeneity (I²> 60%) was present, we did not perform a meta‐analysis (see Assessment of heterogeneity).

Subgroup analysis and investigation of heterogeneity

If sufficient data were available, we conducted the following subgroup analyses for the primary outcomes.

• Age (< 18 years and ≥ 18 years)

• Sex

• Types of interventions

• intact PTH (< 50, 50 to 300, and > 300 pg/mL)

• Concomitant use of vitamin D

Sensitivity analysis

Sensitivity analyses, defined a priori, were performed to assess the robustness of our conclusions. We performed the following sensitivity analyses for the primary outcomes.

• Excluding studies judged to be at a high overall risk of bias

• Excluding studies judged to be at a high or unclear risk of bias for at least one of the overall risk of bias domains.

Summary of findings and assessment of the certainty of the evidence

The main results of the review are presented in the ‘Summary of findings’ tables. These tables presented key information related to the quality of the evidence, the magnitude of the effects of the interventions examined, and the sum of the available data for the main outcomes (Schunemann 2011a). The ‘Summary of findings’ tables also included an overall grading of the evidence related to each of the main outcomes using the GRADE (Grades of Recommendation, Assessment, Development and Evaluation) approach (GRADE 2008; GRADE 2011). This approach defined the quality of a body of evidence as the extent to which one could be confident that an estimate of effect or association was close to the true quantity of specific interest. The quality of a body of evidence involved consideration of the within‐trial risk of bias (methodological quality), directness of evidence, heterogeneity, precision of effect estimates, and risk of publication bias (Schunemann 2011b). We planned to present the following outcomes in the ‘Summary of findings’ tables.

• Incidence of fracture at any sites

• Mean change in the BMD measured using DXA at the femoral neck, total hip, lumbar spine, and distal radius

• Death (any cause)

• Incidence of adverse events

• QoL.