Original remarks by the referee are in square brackets
[Reviewer #1: First of all, although the authors set out to address the issue as to what allows sympatric occurrence of closely related species, the study design does actually not entirely allow for this. Instead, the authors show what could explain the fact that the two sister species do NOT co-occur at equal frequencies.
This is correct and we have changed the title and introduction accordingly
This is a different issue. A study that investigates co-existence of sister species, should focus on the ecology of the two species within sites, and look how the available niche space is partitioned between two species. Although this is alluded to in the discussion, it is not actually tested. The coarseness of part of the data used (i.e. at the 0.5 min level) would not allow for such detailed within-site analysis.]
We do not agree with the reviewer that niche analysis is possible only within site (see e.g. climatic niche analyses), even though we acknowledge that such an analysis could contribute to a more fully understanding of the niche partition. However, this was not primary aim of the study and investigating the factors governing the partitioning of the landscape is also valuable to understand e.g. species ranges.

[Reviewer #1: One aspect allowing co-existence of sister species is reproductive isolation. Although this aspect of the biology of the species is addressed in the present study, I find it not the most exciting aspect of this sister species pair, particularly since previous studies had already suggested pre-zygotic isolation in the field, and demonstrated almost complete post-zygotic isolation in the laboratory. Not finding isolation in laboratory circumstances calls for studies on isolation in nature. The opposite however (i.e. finding almost complete isolation in the lab), does not particularly call for isolation studies in nature as it would be extremely surprising if such isolation would not operate in nature.]
According to our and other lab’s experiences (T. Hankeln & E. Schmidt, Mainz, personal communication), at least some populations of the two species readily produce fertile hybrids in the lab to an extent that requires to breed the species in separate parts of the building in order not to corrupt their genetic integrity. This is also the result of published studies (Keyl & Strenzke 1956). We think it is therefore worthwhile to have a look at the actual isolation in the field, moreover, since the studies of fertility reductions (Hägele 1999) were carried out with laboratory strains that are usually per se less fertile than wild populations (Nowak et al. 2007 Environmental Toxicology & Chemistry 26: 188-192).

[Reviewer #1: Secondly, I have several problems with the methodology applied, listed below:
1. This study samples the study organisms only during one season. The variables that are ultimately suggested to explain the observed pattern, are variables which have been shown to vary extensively during the last decades (e.g. precipitation values). This may result in strong year-to-year differences in population dynamics of the study organisms. Sampling during one season, may simply reflect extreme environmental conditions during that year (e.g. 2003 was an extremely and unusually hot year in western Europe where the organisms were sampled). To use the sampled individuals as a proxy for stable population numbers (which is an implicit assumption in this study) may not be valid. ]
If the actual climate in the year of observation would be the most important factor to influence the distribution, then we shouldn’t have found correlations to long-term parameters. Our approach was therefore rather conservative, with short term fluctuations possibly increasing the error. However, pertaining trends must be therefore particularly strong.

[Reviewer #1: 2. Similarly, the sampling within site is also rather meager. In the Material & Methods section it is stated that within sites a 1 m x 1 m plot was sampled. This means that there is no way of assessing within site variation. As the distribution data are subsequently used in some of the tests in the manuscript, I deem it necessary to get an idea of within-site variation in frequency of distribution.]
Instead of sampling a few sites intensively and assess the within site variation, we have chosen to sample more sites to decrease random error. This is a valid proceeding (Gotelli & Ellison 2004), moreover since we were rather interested in regional scale trends than local effects.

[Reviewer #1: 3. The entire sampling is carried out in a 40 km x 60 km square. This is not a good sample of the distribution range of these species, which is reported to be holarctic. To test whether the variables found to explain the observed pattern are really the most determining variables, a larger part of the ranges of both species should be investigated, ideally spanning the entire distribution ranges. This would also validate better to study macroecological (i.e. climatic) variables which more likely leave a signature at a wider geographical range, than within the plot chosen by the authors. In this light it is in a way surprising that the species have a largely sympatric distribution. Surely, if within the relatively small plot used by the authors macro-ecological variables play such a big role in shaping frequencies of distribution, then - at sites where these variables take more extreme values - complete absence of either one species would be expected. This would lead to a substantial portion of non-overlapping distribution ranges.
4. This study sampled only one season within one year. Given that the climatic variables could affect different parts of the organism's life cycle differently, it would have been more informative to sample throughout the year at each life cycle. This would then have allowed for more detailed discussion as to how the variables found to be significant affect the organisms and the resulting differences in frequency of distribution.]

To 1-4: According to the referee, it appears that we should have sampled the Northern Hemisphere for several years several times per year with within-site spatial replication in order to draw valid conclusions. To our knowledge such a study has never been done with any species. It would have been indeed desirable to do so, however, our resources in terms of money and man-power were unfortunately finite quantities.
As in most ecological studies, the chosen spatial scale determines the possible inferences. We focussed on the landscape level at a scale where distance as such is not yet a limit for dispersal but some variation in environmental parameter might be expected. We think that our conclusions are valid for the spatial scale and location considered and our findings and interpretations are actually not disputed by the referee.

[Reviewer #1: 5. The authors use the relative frequency (of only one of the two species!) to correlate with the 38 selected variables. This assumes that the distribution of that species is entirely shaped by competitive interactions. I would have found it informative to repeat the analyses using absolute numbers for both species, because the relative frequency may still be very high although the actual number of individuals may be very low. This is obviously relevant and should also be taken into account.]
Dealing with the relative frequencies of two species, the rel. freq. of the respectively other species is 1 – first species. This just reverses the signs of the correlation coefficients and is thus redundant information.
Analysing the absolute numbers of individuals per species would yield information on the general suitability of the sites and thus on the absolute niche of each species. To do so properly would have required sampling also sites where both species are absent. Exploring the absolute niche of both species was, however, not the focus of the study.

[Reviewer #1: Should the manuscript be accepted for publication after all, I would like to raise the following issues to consider by the authors to improve readability.

The general issue raised in the paper is put in a context of rather old literature (references from 1859, 1942, 1957, 1967, 1991). Although these include some classical pieces of work, there is surely more recent literature on the subject that could be cited (e.g. the discussion around phylogenetic niche conservatism; Wiens, Evolution 2004). This should ideally be referred to in the introduction as well.]
We have introduced some more recent literature on niche evolution in the introduction.

[Reviewer #1: The notion that the two study species are 'frequently found together at the same sites' suggests that sympatry is the rule. This is contradictory to what is stated in Hägele (1999): "In Europe they can be observed in geographically separated areas, but sympatric populations occur rarely in Germany and The Netherlands..." This disagreement should be addressed.]
Hägele (1999) provides no experimental evidence for this claim and Strenzke (1957) claims the opposite. We have made nevertheless clear that we have referred to the situation encountered in our study region.

[Reviewer #1: There is at present no justification in the manuscript as to why the 38 environmental variables are selected in this study. It would make sense to link these variables to aspects of the organism's biology using references. Hägele (1999) suggests for instance: "...Eco-physiological differences concern temperature and anaerobiotic resistence as well as reactions pressure. It seems as if C. thummi would prefer a more saprobiont habitat than C. piger."]
We have now motivated the choice of parameter groups with the respective Chironomid or other freshwater organism literature.

[Reviewer #1: The first question raised at the end of the introduction ("what is the degree of reproductive isolation in the field?") is only partly addressed by looking at genetic differentiation at the larval stage. Pre-zygotic isolation is thereby left unaddressed. This should be made clear explicitly in the question.]
Genetic differentiation at what developmental stage so ever is an integrative product of all reproductive isolation mechanisms (pre- or postzygotic). We have thus exactly addressed the question posed. What we have not addressed (and never aimed at) is which of all possible reproductive isolation mechanisms are responsible for the observed degree of isolation.

[Reviewer #1: In the Material & Methods, I find the categorization of "Species identification and co-occurrence" under one heading confusing. These two aspects of the study do not form a natural unit.]
Changed according to the referee

[Reviewer #1: In the Material and Methods, for the biologically meaningful climatic parameters, it is not clear from which period these are taken. ]
Information included

[Reviewer #1: Obviously, if they are linked to distribution patterns found in one year, they should ideally be taken from the relevant year when the sampling was done. Given that some are 'mean annual temperature' it is likely that these are means from a larger number of years. At least the relevant value for the year of sampling for these variables should be given (as is done for the soil characteristics which are measured in the same year as the sampling was done). ]
Measuring the microclimate over an entire year at 34 sampling sites would have been certainly desirable, but also way beyond our logistical and financial possibilities. Moreover, it could be argued that species abundance (at least at the beginning of the season) is also a function of the weather in the previous year and so on. Thus, the use of long term climate data averaging over a longer period is probably more suitable to find general trends at the chosen spatial scale. Again, if such long term trends would not influence the species distribution, we shouldn’t have found such correlations.

[Reviewer #1: In figure 1 it would be informative to put circles around species (as inferred from DNA taxonomy). ]
A species delimitation approach has the null hypothesis that there is only a single species (i.e. no separate gene-pools). After the inference of two (or more) good biological species, we linked the species name via chromosome analysis to the delimited entities. Attribution of a taxonomic name at this stage would be thus a premature conclusion.

[Reviewer #1: In figure 3 I can only identify 28 pie charts, whereas in table 1 and in the text of Material and Methods 34 sampling sites are identified. Also, if a black line in a grey chart represents a mixed population (which I assume), much more than about half of the sampling sites contain co-occurring assemblages.]
As detailed in M&M, only sites with at least 7 individuals of piger and/or riparius were taken into account. This reduced the number of sites in these analyses to 29. The black line in the grey charts is an Excel artefact that was removed.

[Reviewer #1: I am surprised by the results of the fisher exact test: looking at the pie charts, I would have expected a non-significant result. I assume that the null hypothesis is that each species occurs in a frequency of 50% at each site. I am not convinced this is a biologically meaningful hypothesis.]
This would be indeed not biologically meaningful. However, the null hypothesis of an exact Fisher-test is not a 50:50 ratio, but an occurrence proportional to the total frequency at all sampling sites, which is equivalent to a random distribution.

[Reviewer #1: In the context of the discussion where it is stated that 'the two taxa conform to several species concepts' it would be interesting to involve into the discussion the species concept that was originally used to describe the two species.]
The species were delineated based on the chromosomal structural differences, as detailed in the introduction. The species description does not explicitly mention a specific species concept (to our experience, this is generally and unfortunately rather the exception in taxonomic literature), so that we should not speculate about the author’s convictions and intentions. .

[Reviewer #1: The conclusion drawn in the discussion that finding the two species less often syntopically due to competitive interaction, could simply be the result of stochastic variation. ]
The statistical tests indicate that the observed pattern is not due to stochastic variation (that’s why we performed them in the first place).

[Reviewer #1: Larger sample sizes are necessary to demonstrate such interactions, as well as ecological experiments. This should at least be mentioned.]
We will indeed now test the hypotheses gain from this study in ecological experiments and have inserted a corresponding notion.

[Reviewer #1: I have problems with the claim that 'this study is the first to demonstrate ecological partitioning among the species pair in the field.' For this a longer term study is necessary + a closer look at how the habitat is partitioned within site, which ultimately determines how the landscape is partitioned.]
Besides that scientific study does not aim to ultimately determine the truth but to test hypotheses, this is the first study with this aim and if nothing else, we do come up with a testable hypothesis how the observed non-random distribution might be explained.

[Reviewer #1: In Table 1 it would be nice to see how many individuals of EACH species are found within site, not just the total number of individuals of both species added up.]
Changed according to the referee

[Reviewer #1: I may misunderstand Table 3, but it seems that for variables such as Mean Prec Wettest Quarter the q-value is actually non-significant at the 0.05 level (q = 0.051). If I understand correctly, q is used as a correction for multiple testing. The resulting values, however, seem then to be misinterpreted as being significant.]
The q-value gives an estimate of the false discovery rate (FDR), i.e. the proportion of false rejections of the null hypothesis and is thus a sensible way to correct for multiple tests. As detailed below Table 3, we are willing to accept one out of ten significance tests to be false by chance (q = 0.1). As with a significance test, this limit is arbitrary, but should be set in advance. A q value cut-off of 0.1 is accepted practice. A q-value of 0.051 is well below this limit and we are thus inclined to believe that the statistical power of this test is sufficient to take this correlation into consideration.