One of the critical clinical decisions made in antiretroviral therapy (ART) is when to switch from an initial regimen to another due to treatment failure. This complex process requires consideration of multiple factors including: (1) what type of monitoring (e.g. clinical, immunologic, virologic) is available to guide switching; (2) establishing criteria for treatment failure (e.g. viral load >10,000 copies/mL); (3) integrating data from different types of monitoring; (4) making a decision; and, if possible, (5) follow-up and monitoring to determine patient outcomes (see Figure 1).
|Figure 1. Decision model for deciding when to switch antiretroviral therapy.|
Figure 1: Decision tree for determining when to switch ART regimens.
The initial step in this model of deciding when to switch is determining what type of monitoring is available and appropriate. Currently, it is not clear which type of monitoring strategy is preferable. This review will seek to find and summarize evidence on optimal monitoring strategies for guiding when to switch first-line regimens among adults and adolescents living with HIV in low-resource settings. This review was one of a series of reviews prepared in 2009 at the request of the World Health Organization to inform the development of new guidelines on ART for adults and adolescents WHO 2009.
Description of the condition
Treatment failure is typically measured in three ways in low-resource settings: (i) clinically, as evidenced by disease progression; (ii) immunologically, as evidenced by trends in CD4 counts over time; and, (iii) virologically, as evidenced by measurement of HIV RNA levels WHO 2006. In settings where viral load is routinely available, treatment failure typically is defined solely by virologic failure.
Description of the intervention
Any intervention/strategy for guiding when to switch ART due to treatment failure of a first-line antiretroviral regimen.
How the intervention might work
Strategies typically will try to (i) increase the likelihood that a regimen is being switched for the correct reason; and, (ii) decrease the likelihood of failing to switch when a switch is warranted.
Why it is important to do this review
Deciding when to switch an ART regimen because of first-line treatment failure is a critical aspect of the management of adults and adolescents on ART. Premature switching can result in unnecessary use of resources. Late switching can result in morbidity and mortality and compromise of future treatment options due to the development of significant antiretroviral resistance.
To assess optimal strategies for guiding when to switch ART regimens due to treatment failure of first-line antiretroviral regimens among adults and adolescents living with HIV in low-resource settings.
Criteria for considering studies for this review
Types of studies
Study inclusion criteria
· Study must evaluate a monitoring intervention/strategy that helps guide when to switch ART
· Randomized controlled trials
· Observational studies (cohort and case-control) which included comparators
· Systematic reviews and meta-analyses (included for review of references and comparison of findings)
Study exclusion criteria
· Letter, editorial, non-systematic review, observational studies without comparators, case report, cross-sectional study design, or descriptive studies
· Studies evaluating ART in patients who have failed more than one regimen
· Studies evaluating substituting rather than switching ART (as described in the WHO 2006 guidelines, substituting is for toxicities and usually involves single-drug changes while switch is due to clinical, immunologic, or virologic failure WHO 2006).
Types of participants
Adolescents and adults living with HIV who have failed on a first-line ART regimen.
Types of interventions
Any strategy/intervention intended to guide health care providers' decision to switch first-line antiretroviral regimens due to treatment failure.
This review looked for all studies with primary comparisons of monitoring strategies (see Table 1). However, comparisons of particular interest were identified a priori: clinical versus virologic, immunologic versus virologic, clinical + immunologic versus virologic, effect of different virologic threshold criteria for failure (e.g. virologic monitoring where criteria for failure was a viral load (VL) > 10,000/mL vs. virologic criteria with VL < 10,000 copies/mL), and role of adherence monitoring in comparisons.
Table 1: Potential comparisons of interest for guiding when to switch.
*While "Other monitoring" strategies were postulated to include other laboratory tests such as hemoglobin, targeted viral load monitoring, and resistance monitoring, this category was left undefined so that the review would be inclusive. A targeted viral load monitoring strategy was noted to be one where viral load monitoring is routinely performed only after clinical and/or immunologic failure has been observed.
Types of outcome measures
2) Morbidity-Centers for Disease Control and Prevention AIDS-defining illness and/or WHO Stage IV
3) Virologic failure-pre-defined concentration of HIV-1 RNA, typically > 400 or 500 copies/mL
4) Immunologic response-geometric mean or median increase in CD4 cell count from baseline
5) Unnecessary switch-participant switched while virologically suppressed
6) Severe adverse events-severe adverse events were classified according to grades 1 to 4 of the Adverse Event Toxicity Scale (Division of AIDS, National Institute of Health) where possible. Using this scale, grades 1 and 2 denote mild to moderate symptoms, grade 3 denotes serious symptoms, and grade 4 denotes life-threatening events requiring significant clinical intervention. Severe adverse events were reported as the proportion of participants that experienced grades 3 and 4 clinical and laboratory adverse events.
1) Development of antiretroviral resistance-genotypic resistance only
2) Missed virologic failure-participant not identified while virologically failing
3) Switch to second-line
4) CD4 Count at Time of Switch (post-hoc outcome added for completeness of reporting)
5) Rate of Switching (post-hoc outcome added for completeness of reporting)
Search methods for identification of studies
We used the HIV/AIDS Cochrane Collaborative Review Group search strategy. We formulated a comprehensive and exhaustive search strategy in an attempt to identify all relevant studies regardless of language or publication status (published, unpublished, in press, or in progress). Full details of the Cochrane HIV/AIDS Review Group methods and the journals hand-searched are published in The Cochrane Library in the section on Collaborative Review Groups (http://www.mrw.interscience.wiley.com/cochrane/clabout/articles/HIV/frame.html). We combined the search strategy developed by The Cochrane Collaboration and detailed in the Cochrane Reviewers' Handbook in combination with terms specific to treatment failure and switching antiretroviral therapy regimens.
Limits. The searches were performed without limits to language, setting or age (though this review focused only on results for adolescents and adults). The searches were limited to human studies published from 1995 (designated start of combination ART era) to July 2009.
Journal and trial databases
· CENTRAL (Cochrane Central Register of Controlled Trials)
· NLM Gateway (for HIV/AIDS conference abstracts before 2005)
· Conference on Retroviruses and Opportunistic Infections, International AIDS Conference and International AIDS Society Conference on HIV Pathogenesis, Treatment, and Prevention from 2005 to 2009,
Clinical trials databases
· ClinicalTrials.gov (http://clinicaltrials.gov/)
· Current Controlled Trials (www.controlled-trials.com/)
· Pan-African Clinical Trials Registry (www.pactr.org)
The following search string was used for MEDLINE:
We used a similar strategy with minor modifications for EMBASE (1995-2009), the Cochrane Controlled Trials Register, which contains mainly reference information to randomized controlled trials and controlled clinical trials in health care, and Gateway, a service of the U.S. National Library of Medicine, which contains conference abstracts. Keywords used for conference abstract searching and clinical trials database searching included the following: treatment failure, switch, and monitoring. There was overlap between the references retrieved in each database. All searches were conducted during July 2009.
Searching other resources
Researchers and relevant organizations. We contacted individual researchers working in the field, such as the AIDS Clinical Trials Group, and policymakers based in inter-governmental organizations including the Joint United Nations Programme on HIV/AIDS (UNAIDS) and WHO to identify trials either completed or ongoing.
Reference lists. We checked the reference lists of all studies identified by the above methods and examined the bibliographies of any relevant systematic reviews, meta-analyses, or current guidelines we identified during the search process.
Data collection and analysis
Selection of studies
LC performed an initial screen of all found titles and abstracts, removing all titles which clearly did not fit inclusion criteria or met exclusion criteria, e.g. editorials, letters, clearly off topic studies. Subsequently, two reviewers (LC and EH) independently reviewed all remaining titles. If the title was believed to be relevant by either reviewer, the corresponding abstract was then reviewed by both authors. If either reviewer felt the abstract was potentially relevant, the full text of the article was then reviewed. Disagreements between the two reviewers were adjudicated by a third reviewer (JH).
Data extraction and management
After initial search and article screening, two reviewers (LC and JH) independently double-coded and entered onto a detailed and standardized data extraction form information from selected studies. Extracted information included:
Study details: citation, start and end dates, location, study design and details.
Participant details: study population eligibility (inclusion and exclusion) criteria, ages, population size, attrition rate, details of HIV diagnosis and disease and any clinical, immunologic or virologic staging or laboratory information, first-line drug regimen details including drug name, dose, and duration, second-line drug regimen details including drug name, dose, and duration.
Interventions details: Clinical, immunologic, virologic and/or other monitoring strategy for switching regimen, frequency of monitoring.
Outcome details: mortality, clinical disease progression (AIDS and non-AIDS events), treatment response (CD4 recovery and VL response), adherence, resistance, adverse events, frequency of switching, time to switch, if patient not switched when meeting criteria what was done (e.g. adherence intervention), unnecessary switches, missed failure.
All relevant data were entered into Cochrane's Review Manager (Version 5).
Assessment of risk of bias in included studies
Application of GRADE and Cochrane Collaboration tools for risk of bias for each individual study was done and presented in summary tables. The GRADE and Cochrane approaches assess risk of bias in individual studies across six domains: sequence generation, allocation concealment, blinding, incomplete outcome data, selective outcome reporting, and other potential biases.
• Adequate: investigators described a random component in the sequence generation process, such as the use of random number table, coin tossing, card or envelope shuffling.
• Inadequate: investigators described a non-random component in the sequence generation process, such as the use of odd or even date of birth, algorithm based on the day or date of birth, hospital, or clinic record number.
• Unclear: insufficient information to permit judgement of the sequence generation process.
• Adequate: participants and the investigators enrolling participants cannot foresee assignment (e.g., central allocation; or sequentially numbered, opaque, sealed envelopes).
• Inadequate: participants and investigators enrolling participants can foresee upcoming assignment (e.g., an open random allocation schedule, a list of random numbers); or envelopes were unsealed or non-opaque or not sequentially numbered.
• Unclear: insufficient information to permit judgement of the allocation concealment or the method not described.
• Adequate: blinding of the participants, key study personnel, and outcome assessor, and unlikely that the blinding could have been broken. No blinding in the situation where non-blinding is not likely to introduce bias.
• Inadequate: no blinding or incomplete blinding when the outcome is likely to be influenced by lack of blinding.
• Unclear: insufficient information to permit judgement of adequacy or otherwise of the blinding.
Incomplete outcome data
• Adequate: no missing outcome data, reasons for missing outcome data unlikely to be related to true outcome, or missing outcome data balanced in number across groups.
• Inadequate: reason for missing outcome data likely to be related to true outcome, with either imbalance in number across groups or reasons for missing data.
• Unclear: insufficient reporting of attrition or exclusions.
• Adequate: a protocol is available which clearly states the primary outcome is the same as in the final trial report.
• Inadequate: the primary outcome differs between the protocol and final trial report.
• Unclear: no trial protocol is available or there is insufficient reporting to determine if selective reporting is present.
Other forms of bias
• Adequate: there is no evidence of bias from other sources.
• Inadequate: there is potential bias present from other sources (e.g., early stopping of trial, fraudulent activity, extreme baseline imbalance, or bias related to specific study design).
• Unclear: insufficient information to permit judgement of adequacy or otherwise of other forms of bias.
Observational studies were assessed for risk of bias using the Newcastle-Ottawa Quality Assessment Scale (NOS) Wells 2009. The NOS is a validated scale from 0 to 9 that uses a ‘star rating system’ and assesses quality of cohort and case-control studies in three main areas: selection of study groups, comparability of study groups and ascertainment of exposure or outcome. See Appendix 1.
The quality of evidence across a body of evidence was assessed with the GRADE approach, defining the quality of evidence for each outcome as, “the extent to which one can be confident that an estimate of effect or association is close to the quantity of specific interest” Higgins 2008. The quality rating across studies has four levels: high, moderate, low, or very low. Randomized trials are categorized as high quality but can be downgraded; similarly, observational studies, which start at low quality, can be upgraded. Factors that decrease the quality of evidence include limitations in study design, indirectness of evidence, inconsistency of results, imprecision of results, or high probability of publication bias. Factors that can increase the quality level of a body of evidence include a large magnitude of effect, if all plausible confounding would reduce a demonstrated effect, and if there is a dose-response gradient (see Table 2).
Table 2: GRADE approach to assessing the quality of evidence across studies.
Note: We specifically considered whether evidence directly addressed low-resource settings in assessing quality of evidence. If the question being addressed only had evidence from high-resource settings, the quality of evidence was downgraded by -1 for Indirectness.
Measures of treatment effect
We used Review Manager 5 provided by Cochrane Collaboration for statistical analysis and GRADEPro 2009 software to produce GRADE evidence profiles and summary of findings tables.
Dichotomous outcomes for effect were summarized in terms of risk ratios (RRs) and numbers needed to treat (NNT) with 95% confidence intervals. Time to event outcomes were summarized in terms of hazard ratios (HRs) with 95% confidence intervals. Observational studies and randomized trials were evaluated separately.
Unit of analysis issues
No significant unit of analysis issues were found.
Dealing with missing data
We contacted authors with requests for missing data.
Assessment of heterogeneity
Heterogeneity among trials was examined using the chi
Assessment of reporting biases
Assessment of publication bias was performed through funnel plots; however, the small number of studies did not allow for definitive conclusions.
Where appropriate, we statistically pooled the outcomes and examined the differences between the two models using random-effects models. Summary statistics using meta-analytic methods were performed, if applicable, and presented in forest plots and GRADE tables.
Subgroup analysis and investigation of heterogeneity
Sub-group analysis was planned for trial quality, setting, and age strata; however, due to the small number of studies, no sub-group analysis was performed.
Due to the small number of studies, no sensitivity analysis was performed by trial quality, setting, or other sub-groups.
Description of studies
Results of the search
From the search strategy, 2,361 titles were initially identified (see Figure 2). LC performed an initial screen of these titles and abstracts, removing all titles which did not fit inclusion criteria or met exclusion criteria, e.g. editorials, letters, clearly off topic studies. This initial screen identified 164 titles. LC and EH then independently conducted the selection of potentially relevant studies by scanning the titles, abstracts, and descriptor terms of all downloaded material from the electronic searches for these 164 studies. Irrelevant reports were discarded, and the full article was obtained for all reports that were potentially relevant or uncertain. LC and EH independently applied the inclusion criteria. JH acted as arbiter where there was disagreement. Studies were reviewed for relevance, based on study design, types of participants, exposures, and outcomes measures. Finally, where resolution was not possible because further information was required, the study was allocated to the list of those awaiting assessment. Attempts were made to contact authors to provide further clarification of data.
|Figure 2. Flow diagram.|
In total, we identified three randomized trials and two observational studies with comparators for data extraction, coding, and potential meta-analysis. Three ongoing trials also were identified.
Home Based AIDS Care (H.B.A.C. 2008, abstract only) is a three-arm randomized trial of the utility of clinical (weekly home visits) versus clinical and immunologic (weekly home visits and CD4 cell counts every 12 weeks) versus clinical, immunologic, and virologic monitoring (weekly home visits and CD4 cell counts and VLs every 12 weeks). It was conducted in Tororo, Uganda and randomized 1,116 total patients enrolled in 2003 and 2004 who were followed a median of three years. The primary outcome was death or any new AIDS-defining illness.
Development of Antiretroviral Therapy in Africa (D.A.R.T. 2009, abstract only) is a randomized trial of laboratory and clinical monitoring (chemistry, full blood count, and CD4 cell count every 12 weeks) versus clinical monitoring (full blood count and chemistry collected and reported to clinician if clinically indicated, CD4 collected but never reported). It was conducted in Uganda and Zimbabwe and randomised 3,316 patients enrolled in 2003 to 2004 who were followed for a median of 4.9 years. The primary outcome was new WHO stage 4 event, death, or serious adverse event.
Observational studies with comparators
Braitstein 2006 or ART-LINC 2006 is a multi-cohort study of 30 ART programs in Africa, Asia, South America, Europe, and North America. This study was primarily intended to compare mortality of ART-naïve HIV-infected persons in the first year of ART between low-income (n=4,810) and high-income countries (n=22,217). However, a substudy analysis compared mortality between low-income ART programs with and without routine monitoring of virologic response. Routine monitoring was not defined in the paper. No adherence data was reported. The amount of follow-up time in each group was not specifically reported.
Egger 2009 or ART-LINC 2009 is a multicohort study of 17 ART programs in low-resource settings comparing programs with (n=7, 13,744 patients) and without (n=10, 6,369 patients) routine VL monitoring (defined as at least one measurement between 3 and 9 months after starting ART in at least 50% of patients). This is the same collaboration as the Braitstein study above. This study analysed 20,113 patients over an unclear time period with outcomes including time to switching and CD4 cell counts at switching. Time to switch analyses were divided into three discrete time periods as the hazard was not proportional over time. No adherence data was reported. The amount of follow-up time in each group was not specifically reported.
Haubrich 2001 is a randomized study of frequent VL (at baseline and every 2 months) compared to infrequent VL monitoring (at baseline and twice yearly). It was conducted by the California Collaborative Treatment Group (CCTG) and consisted of 206 patients enrolled from 1996-1997. Patients were randomized (1.5:1) and the primary outcome was HIV RNA reduction at six months. This study was excluded because it compared effects of different frequencies of one type of monitoring rather than comparing one distinct monitoring strategy to another. This study also did not compare different VL thresholds for switching.
Ongoing randomized trials
Lallemant (NCT00132682) is an ongoing randomized, multi-center study of adults in Thailand to determine if a decision to switch to a subsequent ART regimen based upon CD4 count (switch with confirmed 30% CD4 decline from baseline within 200 cells/μL from baseline) rather than based on VL (switch with confirmed VL > 400 copies/mL) could ensure the same immunological and clinical outcomes while preserving future treatment options.
Laurent (NCT00301561) is on ongoing randomized, multi-center trial of adults in nine rural district hospitals in Cameroon evaluating outcomes of a clinical and immunologic approach (VL and CD4 count every six months and clinical monitoring by physicians) versus a public health (clinical monitoring only) approach (clinical monitoring by nurses and physicians only) to the provision of ART.
Sagg (NCT00929604) is an ongoing randomized trial of adults in Lusaka, Zambia evaluating the use of targeted VL monitoring (VL performed if criteria for either immunologic or clinical failure met) versus routine VL monitoring (VL monitoring at 3, 6, 12, 18, 24, 30, and 36 months) to improve survival and decrease HIV disease progression in patients receiving ART.
PENPACT1 (NCT00039741) is an ongoing randomized, open-label, multi-country study of ART and treatment-switching strategies (switching therapy at VL thresholds of 1,000 copies/mL vs. 30,000 copies/mL) in ART-naïve children and adolescents >30 days and <18 years of age).
Risk of bias in included studies
|Figure 3. Methodological quality summary: review authors' judgements about each methodological quality item for each included study.|
|Figure 4. Methodological quality graph: review authors' judgements about each methodological quality item presented as percentages across all included studies.|
No information was available for either study on the allocation process.
Appropriately, neither study had participants or personnel blinded to the intervention. It is not clear whether outcome assessors were blinded in either study. There exists a reasonable chance for potential bias due to lack of blinding. For example, providers for patients receiving less intensive monitoring may have chosen to provide different care than providers of patients with immunologic and/or virologic monitoring. There is no clear evidence for bias found in the current reports, however, and the overall likelihood of bias from not blinding is probably low. Full publication may help clarify whether outcome assessors were blinded.
Incomplete outcome data
Both studies were reported in abstract form only at the time this review was performed. Full publication of results is still pending. Therefore, currently there is incomplete outcome data reporting with loss to follow-up analyses not extensively presented (although absolute numbers were small).
Both studies were reported in abstract form only at the time this review was performed. Full publication of results is still pending. It is difficult to assess from the abstract presentations alone if all outcomes were reported. Therefore, it appears that more complete reporting from both included studies could exist.
Other potential sources of bias
There are no clear sources for other potential bias.
Risk of Bias-Observational Studies
Two observational studies (ART-LINC 2006 and 2009) were included in final analysis of observational study characteristics and methodological quality (see Table 3).
Table 3: Newcastle-Ottawa quality assessment scale for included observational studies.
Comments: Selection of non-exposed cohort for both studies was not drawn from the same community as the exposed cohort. While adjusting did occur for age, sex, clinical stage, and CD4 cell count at baseline (most important factor), but not for other potential factors such as program characteristics. Follow-up was variable in both studies for the primary outcomes.
Effects of interventions
Of the evidence available, three comparisons were studied: clinical versus immunologic and clinical monitoring; clinical versus virologic, immunologic, and clinical monitoring; and immunologic and clinical monitoring versus virologic, immunologic, and clinical monitoring. GRADE evidence profiles were created for each of these comparisons. See Figure 6, Figure 5, Figure 7, and Figure 8.
Clinical vs. Immunologic and Clinical Monitoring. Based upon two randomized trials including 4,064 patients, clinical monitoring alone results in increased mortality (HR 1.35, 95% (confidence interval) CI 1.12-1.63, low-quality evidence), increased AIDS-defining illnesses and mortality as a composite endpoint (HR 1.33, 95% CI 1.16-1.51, moderate), no difference in serious adverse events (data from DART study only, HR 1.12, 95% CI 0.95-1.31, low), increased numbers of unnecessary switches (data from HBAC study only, RR 30.5, 95% CI 1.83-508, low), and no difference in switches to second-line (RR 1.73, 95% CI 0.37-8.06, low) compared to immunologic and clinical monitoring. Significant statistical heterogeneity was found for the outcome of switches to second-line (I
Clinical vs. Virologic, Immunologic, and Clinical Monitoring. Based upon a single randomized trial including 745 patients, clinical monitoring alone results in a trend toward increased mortality (HR 1.58, 95% CI 0.97-2.60, low), increased AIDS-defining illnesses and mortality as a composite endpoint (HR 1.88, 95% CI 1.25-2.84, low), increased unnecessary switches (RR 30.3, 95% CI 1.82-504, low), no difference in virologic treatment failures (RR 1.16, 95% CI 0.61-2.22, low), and a trend towards an increase in switches to second-line (RR 2.37, 95% CI 0.99-5.65, low) compared to virologic, immunologic, and clinical monitoring.
Immunologic and Clinical vs. Virologic, Immunologic, and Clinical Monitoring. Based upon a single randomized trial including 739 patients, immunologic and clinical monitoring results in no difference in mortality (HR 1.14, 95% CI 0.69-1.89, low), no difference in AIDS-defining illnesses and mortality as a composite endpoint (HR 1.28, 95% CI 0.84-1.97, low), no difference in unnecessary switches (no unnecessary switches in either group, very low), no difference in virologic treatment failures (RR 1.61, 95% CI 0.88-2.95, low), and no difference in switches to second-line (RR 0.57, 95% CI 0.17-1.92, low) compared to virologic, immunologic, and clinical monitoring. Observational studies appear to demonstrate that programs with virologic, immunologic, and clinical monitoring switch therapy more frequently (RR 1.60, 95% CI 1.35-1.89, very low), and earlier (time of switch 7-18 months, HR 1.38, 95% CI 0.97-1.98; 19-30 months, HR 0.97, 95% CI 0.59-1.60; 31-42 months, HR 0.29, 95% CI 0.11-0.79, very low), and at higher CD4 counts (mean of 161 cells/μL vs. 141 cells/μL, very low) compared to programs with only immunologic and clinical monitoring.
See Figure 5, Figure 6, Figure 7, Figure 8, Figure 9, Figure 10, Figure 11, Figure 12, Figure 13, Figure 14, Figure 15, Figure 16, Figure 17, Figure 18, Figure 19, Figure 20, Figure 21, Figure 22, Figure 23, Figure 24, and Figure 25.
|Figure 5. Forest plot of comparison: 1 Clinical Monitoring vs Immunologic Monitoring and Clinical Monitoring, outcome: 1.1 Mortality.|
|Figure 6. Forest plot of comparison: 1 Clinical Monitoring vs Immunologic Monitoring and Clinical Monitoring, outcome: 1.3 AIDS-defining illness or Mortality.|
|Figure 7. Forest plot of comparison: 1 Clinical Monitoring vs Immunologic Monitoring and Clinical Monitoring, outcome: 1.4 Serious Adverse Event.|
|Figure 8. Forest plot of comparison: 1 Clinical Monitoring vs Immunologic Monitoring and Clinical Monitoring, outcome: 1.5 Unnecessary Switch (Switch to Second-line with Undetectable Viral Load).|
|Figure 9. Forest plot of comparison: 1 Clinical Monitoring vs Immunologic Monitoring and Clinical Monitoring, outcome: 1.7 Switch to Second-Line.|
|Figure 10. Forest plot of comparison: 2 Clinical Monitoring versus Virologic, Immunologic, and Clinical Monitoring, outcome: 2.1 Mortality.|
|Figure 11. Forest plot of comparison: 2 Clinical Monitoring versus Virologic, Immunologic, and Clinical Monitoring, outcome: 2.3 AIDS-defining illness or Mortality.|
|Figure 12. Forest plot of comparison: 2 Clinical Monitoring versus Virologic, Immunologic, and Clinical Monitoring, outcome: 2.4 Unnecessary Switch (Switch to Second-line with Undetectable Viral Load).|
|Figure 13. Forest plot of comparison: 2 Clinical Monitoring versus Virologic, Immunologic, and Clinical Monitoring, outcome: 2.5 Virologic Treatment Failure.|
|Figure 14. Forest plot of comparison: 2 Clinical Monitoring versus Virologic, Immunologic, and Clinical Monitoring, outcome: 2.6 Switch to Second-line.|
|Figure 15. Forest plot of comparison: 3 Immunologic and Clinical Monitoring versus Virologic, Immunologic, and Clinical Monitoring, outcome: 3.1 Mortality.|
|Figure 16. Forest plot of comparison: 3 Immunologic and Clinical Monitoring versus Virologic, Immunologic, and Clinical Monitoring, outcome: 3.3 AIDS-defining illness or Mortality.|
|Figure 17. Forest plot of comparison: 3 Immunologic and Clinical Monitoring versus Virologic, Immunologic, and Clinical Monitoring, outcome: 3.4 Unnecessary Switch (Switch to Second-line with Detectable Viral Load).|
|Figure 18. Forest plot of comparison: 3 Immunologic and Clinical Monitoring versus Virologic, Immunologic, and Clinical Monitoring, outcome: 3.5 Virologic Treatment Failure.|
|Figure 19. Forest plot of comparison: 3 Immunologic and Clinical Monitoring versus Virologic, Immunologic, and Clinical Monitoring, outcome: 3.6 Switch to Second-Line.|
|Figure 20. Forest plot of comparison: 4 Immunologic and Clinical Monitoring vs Virologic, Immunologic, and Clinical Monitoring-Observational Studies, outcome: 4.1 Mortality.|
|Figure 21. Forest plot of comparison: 4 Immunologic and Clinical Monitoring vs Virologic, Immunologic, and Clinical Monitoring-Observational Studies, outcome: 4.2 Rate of switching.|
|Figure 22. Forest plot of comparison: 4 Immunologic and Clinical Monitoring vs Virologic, Immunologic, and Clinical Monitoring-Observational Studies, outcome: 4.3 Time to switch (7-18 months f/u).|
|Figure 23. Forest plot of comparison: 4 Immunologic and Clinical Monitoring vs Virologic, Immunologic, and Clinical Monitoring-Observational Studies, outcome: 4.4 Time to switch (19-30 months f/u).|
|Figure 24. Forest plot of comparison: 4 Immunologic and Clinical Monitoring vs Virologic, Immunologic, and Clinical Monitoring-Observational Studies, outcome: 4.5 Time to switch (31-42 months f/u).|
|Figure 25. Forest plot of comparison: 4 Immunologic and Clinical Monitoring vs Virologic, Immunologic, and Clinical Monitoring-Observational Studies, outcome: 4.6 CD4 count at switch.|
Summary of findings tables for each comparison are shown in Figure 26, Figure 27, Figure 28, and Figure 29. GRADE evidence profiles for these comparisons are also available and can be found on the following Cochrane HIV/AIDS Group web site: http://www.igh.org/Cochrane/GRADE
|Figure 26. Immunologic and Clinical Monitoring versus Virologic, Immunologic, and Clinical Monitoring|
|Figure 27. Immunologic and Clinical Monitoring versus Clinical Monitoring|
|Figure 28. Virologic, Immunologic, and Clinical Monitoring versus Clinical Monitoring|
|Figure 29. Virologic, Immunologic, and Clinical Monitoring versus Clinical and Immunologic Monitoring|
Summary of main results
Despite a comprehensive search, a limited number of studies were identified which addressed this topic, and, of the two randomized trials identified, both were in abstract form only when the literature search was conducted. Observational studies were also limited in number and of lesser quality. While the quality of the evidence was variable from the randomized trials, ranging from very low to moderate, there appeared to be substantial benefits for key outcomes (e.g. mortality, AIDS-defining illness and mortality as a composite endpoint, and unnecessary switches) favoring both immunologic and clinical monitoring or virologic, immunologic, and clinical monitoring versus clinical monitoring alone. Very low-quality evidence from observational studies suggested that virologic, immunologic, and clinical monitoring led to more frequent switching, earlier switching, and switching at higher CD4 counts compared to immunologic and clinical monitoring.
It is interesting to note that in the observational ART-LINC study there was a higher rate of switching when virologic monitoring was used compared to immunologic and clinical monitoring. In the RCT HBAC study where virologic monitoring was used, there were no differences seen in the numbers of switches to second-line comparing virologic, immunologic, and clinical monitoring to immunologic and clinical monitoring. However, there was a strong trend toward more frequent switches in the clinical monitoring-alone arm. The reasons for these findings are not clear, although in HBAC the impetus to switch may have been high in the setting of clinical failure without any laboratory data to support not switching and where access to second-line was equally available in both study arms. In ART-LINC, as cohorts were being compared to one another, second-line ART access as well as adherence, clinical, and immunologic monitoring may have been significantly different from cohort to cohort, thus influencing the switching of patients to second-line therapy.
No significant statistical heterogeneity was found except for the outcome of switch to second-line comparing clinical versus immunologic and clinical monitoring. The HBAC study had significantly more switches to second-line in the clinical monitoring-alone arm, while the DART study had significantly fewer switches to second-line in the clinical monitoring-alone arm. The reason for these contrasting estimates of effect is unclear, but could be related to different lengths of follow-up (the DART study had longer follow-up and switching to second-line could be an outcome that interacts with time on ART), different initial baseline ART regimens being used, differences in criteria for immunologic failure, and differences in provider decision-making. Due to this heterogeneity, it may not be appropriate to combine these estimates of effect into a summary estimate.
While immunologic and/or virologic monitoring appears to have benefits in guiding when to switch ART compared to clinical monitoring alone, there remain many areas of uncertainty. For example, there remains no standarized definition for routine VL monitoring. In the HBAC study viral loads were performed every three months, in contrast to the observational studies where routine viral load monitoring was defined as at least one measurement between three and nine months after starting ART in at least 50% of patients. Further complicating the issues of VL monitoring and immunologic monitoring is that these types of monitoring may have different effects based upon when they are performed in relation to time from ART initiation. That is, virologic or immunologic monitoring done 2-3 years after ART initiation may have very different purposes and impact than monitoring done six months after ART initiation. For example, VL monitoring could be used at six months after ART initiation primarily to assess adherence compared to virologic monitoring performed years after ART initiation to investigate the need for switching to second-line ART.
The benefits of these interventions also must be considered in the context of their associated costs, and future cost-analysis will improve from having these randomized trials data incorporated into their models. Also, the processes explaining the benefits of immunologic and/or virologic monitoring over clinical monitoring alone deserve further exploration. It has been postulated that earlier switching in the immunologic monitoring arm of the DART trial was the underlying reason for clinical benefit; however, this finding has not been reported from the HBAC trial D.A.R.T. 2009, H.B.A.C. 2008. Finally, further investigations into the role of virologic monitoring, particularly what benefits it may have over immunologic monitoring, if any, are needed and trials addressing this issue are ongoing. Targeted VL monitoring, where VLs are performed to confirm treatment failure in the setting of clinical and/or immunologic failure, is a one promising variant of virologic monitoring in need of further study Sagg.
The decision to switch first-line ART due to treatment failure is challenging and based on many factors, involving issues not related only to types of monitoring. For example, the diagnostic accuracy of criteria for treatment failure, either using clinical or immunologic-based standards, remain imperfect, and the most appropriate criteria still are not agreed upon Elliott 2008. The role of adherence interventions and monitoring has also been inadequately addressed, and further studies addressing this area would be informative Orrell 2007.
The question of "when to switch" is of fundamental importance to the management of ART and has significant implications in terms of the sustainability and quality of ART in low-resource settings. Continued research efforts in this area are critical and will help build the evidence base for this challenging decision-making process.
Overall completeness and applicability of evidence
Further information on the studies currently reported in abstract form will be insightful. Ongoing studies addressing this topic will likely contribute substantially to the evidence on optimal monitoring strategies for guiding when to switch first-line therapy. Cost-analysis studies will lend further insights into the applicability of these findings to low-resource settings and provide context for these interventions. It should be noted that after our literature search was completed, one of the included studies was published in a peer-reviewed journal DART 2010. An informal assessment of this publication did not find any significant differences from the data used in this review. The HBAC study, originally presented in 2008, remains unpublished.
Quality of the evidence
See summary of main results.
Potential biases in the review process
The utilization of data published in abstract form only and/or presented orally at conferences may not represent the full picture of evidence for these studies. Publication bias was minimized by a comprehensive search strategy that included evaluating published and unpublished literature.
Agreements and disagreements with other studies or reviews
There are no other studies or systematic reviews addressing this topic that we are aware of at this time.
Implications for practice
This review supports the use of immunologic and/or virologic monitoring to help optimally guide switching first-line antiretroviral regimens because of treatment failure in adults and adolescents in low-resource settings. However, further evidence, peer-reviewed publication of the studies used in this review, and cost-analysis studies for contextualization will be needed to solidify these findings.
Implications for research
There are ongoing studies that will lend further insights into this research question. Additional studies and peer-reviewed publication of the studies used in this review will be helpful in deepening the evidence base. However, as noted in the decision algorithmn initially presented, there are a multitude of potential strategies to help guide decisions on when to switch, and current and ongoing studies are needed to address the entire range of potential options. Further investigations of novel options may be informative. In particular, additional work on the most appropriate criteria for treatment failure are needed.
Gail Kennedy, George Rutherford, Alicen Spaulding, Nandi Siegfried, and Tara Horvath of the Cochrane HIV/AIDS Group for their support and advice. Joy Oliver for research assistance.
Data and analyses
- Top of page
- Authors' conclusions
- Data and analyses
- What's new
- Contributions of authors
- Declarations of interest
- Sources of support
- Differences between protocol and review
- Index terms
Appendix 1. Newcastle-Ottawa quality assessment scale for cohort studies.
Assessment of risk of bias for individual observational studies
Observational studies were assessed for risk of bias using the above criteria in Table 9 and also the Newcastle-Ottawa Quality Assessment Scale (NOS) (Wells 2009). The NOS is a validated scale from 0 to 9 that uses a ‘star rating system’ and assesses quality of cohort and case-control studies in three main areas: selection of study groups, comparability of study groups and ascertainment of exposure or outcome.
Note: A study can be awarded a maximum of one star (*) for each numbered item within the Selection and Outcome categories. A maximum of two stars can be given for Comparability.
1) Representativeness of the exposed cohort
a) truly representative of the average _______________ (describe) in the community *
b) somewhat representative of the average ______________ in the community *
c) selected group of users, eg nurses, volunteers
d) no description of the derivation of the cohort
2) Selection of the non exposed cohort
a) drawn from the same community as the exposed cohort *
b) drawn from a different source
c) no description of the derivation of the non exposed cohort
3) Ascertainment of exposure
a) secure record (eg surgical records) *
b) structured interview *
c) written self report
d) no description
4) Demonstration that outcome of interest was not present at start of study
a) yes *
1) Comparability of cohorts on the basis of the design or analysis
a) study controls for _____________ (select the most important factor) *
b) study controls for any additional factor « (This criteria could be modified to indicate specific control for a second important factor.)
1) Assessment of outcome
a) independent blind assessment *
b) record linkage *
c) self report
d) no description
2) Was follow-up long enough for outcomes to occur
a) yes (select an adequate follow up period for outcome of interest) *
3) Adequacy of follow up of cohorts
a) complete follow up - all subjects accounted for *
b) subjects lost to follow up unlikely to introduce bias - small number lost - > ____ % (select an adequate %) follow up, or description provided of those lost) ?
c) follow up rate < ____% (select an adequate %) and no description of those lost
d) no statement
Last assessed as up-to-date: 30 September 2009.
Review first published: Issue 4, 2010
Contributions of authors
All authors contributed to the design and conduct of this study, as well as with manuscript drafting and submission. LC and JH produced the GRADE tables.
Declarations of interest
We declare that we have no conflicts of interest.
Sources of support
- Cochrane HIV/AIDS Group, University of California, San Francisco, USA.
- Centers for Disease Control and Prevention (CDC), USA.Cooperative Agreement #U2GPS001468, "Atlanta HQ UCSF Technical Assistance to Support the President's Emergency Plan for AIDS Relief" from the Centers for Disease Control and Prevention (CDC), with funds from National Center for HIV, Viral Hepatitis, STDs and TB Prevention (NCHSTP). Its contents are solely the responsibility of the authors and do not necessarily represent the official views of CDC.
- World Health Organization, Switzerland.World Health Organization #200106621, Systematic reviews and development of GRADE profiles, based on the new WHO GRC guidelines, for the "WHO Guidelines on antiretroviral therapy for HIV infection in adults and adolescents - 2009 revision."
Differences between protocol and review
No significant differences are noted.
Medical Subject Headings (MeSH)
MeSH check words
Adolescent; Adult; Humans; Young Adult