Referee 1's review:

Comments for Authors: Prospects for sustainable malaria control in areas of mesoendemic transmission in sub-Saharan Africa

This paper presents a mathematical model for malaria transmission which incorporates in a simplified way the development of immunity to clinical disease through a second class of infection. The most interesting results lie in the ideas of bistability which could impact on the measurement of success of eradication programmes. However, at present it is not clear whether these results depend on some of the main simplifying assumptions that have been made. In addition, the paper is written in a brief, but still rather technical manner, which would limit its wider readership.

Main points:
1. The model of immunity presented here is similar to those already published some time ago (see for example the collection of papers in Anderson & May 1982). The authors mention briefly in the discussion some other models. However, it was not clear to me in this manuscript whether the current model differed significantly from the earlier models and it would be helpful for the authors to include a section detailing the main differences.
2. The authors appear to have chosen to ignore the mosquito section of the transmission dynamics cycle. They may have good reasons for doing so but again these are not given. It would be useful to see the results also presented with such dynamics to convince the reader that the main results of the paper still hold if realistic malaria dynamics are considered.
3. The authors attempt to fit the model to clinical disease data stratified by age from a variety of different settings . These estimates are substantially higher than estimates from the same sites published some time ago for severe malaria (see Gupta et al. 1999 Nature Medicine). For example, Kilifi is 19.87 here and 0.6-1.12 in Gupta et al. Similarly Siaya is 71.02 here and 2.11 there. Whilst there will clearly be a difference between severe disease and all hospital admissions, the difference still appears rather large and there appears no obvious scaling factor between the two studies. Could the authors comment on this?
4. The authors present estimates of other parameters such as the duration of clinical disease and less severe infection. The confidence limits here reflect uncertainty only within the model structure proposed. However, as noted on p410 of Anderson & May 1991, "observed curves can be fitted by a wide variety of models that contain very different assumptions". I suspect that here the model being presented, which does not incorporate any functional understanding of the acquisition of clinical immunity, may be giving erroneous estimates (particularly in relation to the force of infection). Put another way, the authors attempt to fit too many parameters for the data; instead they should be looking at other sources of data to inform parameters such as the duration of disease and infection (e.g. the Garki project) so that the parameters they do fit are consistent with current understanding of malaria transmission.
5. The most interesting and novel section of the paper is the bistability results. I would recommend that the authors focus to a greater extent on these as they have obvious implications for eradication programmes. Whilst interesting, Figure 3 would lose most of the non-technical readership thereby reducing the impact of the paper. Also the text on this section could be expanded to give the non-technical reader a better sense of what this means - this would greatly increase the accessibility of the paper.

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N.B. These are the comments made by the referee when reviewing an earlier version of this paper. Prior to publication the manuscript has been revised in light of these comments and to address other editorial requirements.