mishra-lab / sr-heterogeneity-hiv-models Goto Github PK

The references in the supplementary materials are incorrectly formatted. Often they give the second initial of the author but not the first initial. For example, L. Korenromp (reference 62) should be E.L. Korenromp, and J. Abu-Raddad (reference 56) should be L.J. Abu-Raddad.

Whilst recognising this is a scoping review, some more discussion on the impact of these findings for the global HIV response would be welcome. As noted in the discussion, modelled estimates "did not always reflect the available data". The key population estimates (and subsequent estimates of averted HIV transmission) are reliant on weak data and some informed comment on how these results should be used would be good.

Consider inserting Table C.1 into the main text

Please elaborate on and support Figure C.11 - it's not immediately clear to me that 'the pattern of incidence reduction versus modelled heterogeneity was similar to the pattern of infections averted versus modelled heterogeneity". Recognising that these data do not stem from the same studies, it is noted that in Table C.1 the incidence reduction increases ~2fold between no risk heterogeneity and activity (no KP), whilst averted infections decreases ~4fold. This would appear to be a key difference?

I felt there could have been more explanation for some of the unexpected findings in Table C1. As noted earlier, some of these odd findings might just be due to inappropriate statistical tests.

Further discussion of the headline finding would be welcome - that the omission of key populations but the inclusion of risk heterogeneity in the generalised population brings about the smallest declines in new HIV infections is notable. Where possible - interrogating which dynamics are most important in the discrepancy between 'Activity (no KP)' and the other three model scenarios would be of interest.

It was not clear why the authors excluded individual-based approaches from this review. Although people tend to use the terms 'compartmental models' and 'deterministic models' interchangeably, some would argue the terms mean slightly different things (see Garnett, STIs, 2002, 78:7-12). The point is that it's possible for an individual-based model to be 'compartmental' in the sense that it works with categorical variables rather than continuously-defined variables. In such cases one could argue for including an individual-based model in the review, since its compartments/categories can be classified in the same way as a deterministic model. But even when key variables are defined on a continuous scale it's not clear why you would want to exclude the individual-based model from the review.

Given that the results from Table C1 are so central to the overall conclusion of the paper (and are referred to in the abstract), it seems strange to put this table in the supplementary materials. I think it would be more appropriate to include this table in the main text of the article.

A related concern is that the tests for statistically significant differences in the univariable analysis appear problematic. When you use the Kruskal-Wallis test you are assuming independence of observations. But here the observations are not statistically independent of one another - in many cases multiple observations are being taken from the same study (and there is likely to be a high degree of within-study correlation). By not taking into account the within-study correlation I think you exaggerate the significance of the differences between model types. That might explain some of the odd results in Table C1 (for example a statistically significant positive relationship between HCT behaviour change and the incidence reduction, but a significant negative relationship between HCT behaviour change and the cumulative % of infections averted). If you use a meta-regression approach, you should be able to control for the within-study correlation.

Page 6: I didn't understand this sentence: "Studies in Dataset B specifically examined scale-up of ART coverage alone (versus combination intervention) for the whole population (versus ART prioritized to subgroups)". The authors seem to be referring to multiple different comparisons in the same sentence. Perhaps it would help to rewrite as two sentences, focusing on the primary comparison of interest in the first sentence.

Consider a sensitivity analysis of the main findings without South African data

Do any studies address the age distribution of key populations? This would be useful to include

I find the bubble plots difficult to interpret. The bubbles are often similarly sized, I'm not sure the extra information adds to the results and crowds the plot. Perhaps grouped bar charts or grouped box plots would be easier to read - particularly for Figure 3.

After finalizing revisions.

Were transgender people or prisoners included in any studies?

A limitation of this review, which the authors acknowledge, is that it is essentially an ecological analysis. Although there is an association between models allowing for heterogeneity in risk behaviour and models predicting smaller ART impacts on HIV incidence, this finding doesn't necessarily prove that heterogeneity in risk behaviour determines the extent of the ART impact. There are many possible confounders and other variables that influence the extent of the modelled reductions in HIV incidence, as the authors note. Would it not make more sense to use a meta-regression approach to isolate the effect of the heterogeneity assumptions, controlling for the confounding factors? Although this wouldn't completely get around the causality conundrum, it would be better than the current approach, which is effectively relying on univariable rather than multivariable analysis.

It's not immediately clear to me what the key recommendation is that flows from Figure 3. If I have a model with the base case (no risk heterogeneity), which compartments or dynamics should I add first better to represent the true epidemic?

The third paragraph of the Introduction mentions possible inequalities in uptake of HIV testing and ART as an explanation for the lower-than-expected impact of UTT, and mentions a number of sub-populations that might be disadvantaged. But the authors fail to mention heterosexual men. There is much evidence of heterosexual men being at a disadvantage (in terms of HIV testing and ART uptake) and they also contribute more to transmission than heterosexual women, so why are they not mentioned here? Similarly in the second and third paragraphs of the discussion the authors criticize modelling studies that don't consider key population dynamics, but they don't mention the challenges around engaging heterosexual men (and the problem that many models don't consider differences between men and women in ART coverage). The poor uptake of HIV testing and ART in heterosexual men is really the Achilles heel in the 'treatment as prevention' strategy in Africa, yet this issue is frequently ignored in the literature. I feel the authors could have drawn more attention to this issue throughout the paper, rather than focusing narrowly on the traditionally defined key populations.

Although the authors explain why modelling key populations might influence the predicted impact of ART on HIV incidence, I think the introduction would be strengthened if they also mentioned the literature that covers heterogeneity more broadly - and the role that heterogeneity plays in determining intervention impact. For example, Nagelkerke et al (2007, BMC Infectious Diseases, 7:16) showed that the modelled impact of male circumcision on HIV incidence was much greater when assuming no heterogeneity in risk behaviour, Johnson et al (2012, Journal of the Royal Society Interface, 9:1544-54) showed that the modelled impact of condoms and ART was strongly correlated with the heterogeneity in risk behaviour, and Hontelez et al (2013, PLoS Medicine, 10:e1001534) showed that allowing for heterogeneity reduced the predicted impact of ART on HIV incidence. Key populations are one component of the heterogeneity-impact relationship, but the introduction currently reads as if they are the only determinant of the relationship.

Figure 2: I would prefer HIV prevalence over PLHIV as the chloropleth

As HIV prevalence is linked to epidemic type, it's interesting that ART prevention impacts were larger with lower HIV prevalence. As the lower prevalence epidemics in West Africa are driven by KPs/more so than the epidemics in ESA, I assume that modelling studies in West Africa are more likely to be KP-disaggregated. However, you have shown that KP-disaggregated models estimate smaller ART prevention impacts. Could this be explored further?

Page 17: "Our ecological analysis also suggested that the anticipated ART prevention impacts from homogeneous models may be achievable in the context of risk heterogeneity if testing/treatment resources are prioritized to higher risk groups." I didn't follow this - what is this based on? The comparison of the 21% vs 10% on p. 15? If so, aren't the numbers too small to suggest a statistically significant difference? (See my earlier comment on testing for significant differences.)