General
This study reports on an evaluation of consultation rates of ILI in the outpatient and GP settings for early detection of influenza epidemics in a subtropical city. The authors adopted the wavelet analysis and concluded that consultation rates of ILI could provide at least two weeks early warning of influenza epidemics as indicated by laboratory-based surveillance of influenza viruses.

This manuscript is an interesting and well-written paper, which attempted to answer a question of public health importance. However, I have major methodological concerns over the appropriateness of using wavelet analysis in terms of assessing the timeliness of ILI consultation rates compared with influenza virus isolation rates from laboratories. Detailed comments on this point are provided in the response to question 2 below.

Overall, it is my opinion that the wavelet analysis is not an adequate statistical method to answer this particular question of interest. However, I would like to offer the authors an opportunity to address this issue.

Key questions to be considered
1. What are the main claims of the paper?
This study is claimed to have found that consultation rates of ILI could provide at least two weeks early warning of influenza epidemics as indicated by laboratory-based surveillance of influenza viruses.

2. Are the claims properly placed in the context of the previous literature?
There is a fundamental flaw in using the wavelet analysis to reach this claim. The reasons are two folds:
Firstly, although this manuscript reference a number of papers that used the wavelet analysis, it seems to me that they explored very different questions compared with this paper. For examples, Brontin et al (2005) evaluated the impact of pertusis vaccination, which is very specific to a particular etiology. In contrast, ILI is not specific to influenza virus and can be caused by a variety of organisms. When comparing two time series, particularly in the situation where you are not sure whether the two series represent the same thing, it is important to take into account temporal confounders, such as longer term trend, calender effect (holiday and day-of-week) and autocorrelation. The danger of ignoring these temporal confounders when assessing temporal relationship between two time series was robustly demonstrated by Bowie and Prothero (1981 Int J Epidemiol).

Secondly, as argued by Viboud et al (2006), the authors argued that the excess activity (eg. influeza and pneumonia mortality) over and above seasonal background is an useful indicator of timing of epidemics. In another words, the short-term variations rather than the longer term trends are more important for assessing the timeliness between time series. In this manuscript, only the annual cycles were examined when assessing timeliness. How would the timeliness based on annual seasonal cycles that reported in this manuscript be translated into daily or weekly surveillance?

3. Do the experimental data support the claims? If not, what other evidence is required?
Yes.

4. Who would find this paper of interest? And why?
The question that this manuscript tried to answer would be of an interest to public health professionals who are interested in public health surveillance, particularly in the fields of syndromic surveillance and early warning outbreak detection systems. Also this question could be of an interest to broader public health audiences.

5. In what further directions would it be useful to take the current research?
See the comments for question 2.

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N.B. These are the general comments made by the reviewer when reviewing this paper in light of which the manuscript was revised. Specific points addressed during revision of the paper are not shown.