FishPro, a division of HDR

January 2003

Review of Hedgecock et al. 2002: Documenting Biodiversity of Coastal Salmon (Oncorhynchus spp.) in Northern California, Final Report, December 2002

By CHRIS BEASLEY, principal author

PART I: COHO SALMON ANALYSES

Introduction

In general the researchers have made an impressive effort to elucidate the relationship among coho salmon spawning aggregates in California. That being said, a more detailed account of sampling effort is desperately needed. Throughout the report, the authors note that only juvenile samples were available from some spawning aggregates, and in many cases, the total sample size of those juvenile groups was small. In order to determine whether the results of the analyses are biologically meaningful, the reader must know if sample sizes and sampled life history stages were limited by sampling effort or actual abundance. For example, were temporal replicates from spawning aggregates not available because no one attempted to collect them, or because fish were not encountered after exhaustive sample efforts? Given this limitation, the only meaningful comments that I can make regarding this research are methodology based.

I have grouped comments into three categories: statistical, biological, and interpretation of results.

Statistical Evaluation

The researchers have employed several methods to statistically compensate for small sample sizes and less than ideal distributions of sampled life history stages. However, there are some details that could be profitably expanded upon. For example, a general discussion of marker selection, the assumptions of some of the methods, as well as the potential for utilizing alternative analyses should be included.

The researchers screened some 67 micro satellites from which they selected seven for use in their study of coho salmon. This represents a substantial effort, however it is not entirely clear why some loci were excluded, or why only seven loci were selected. I am not suggesting that the selected loci were insufficient, only that some discussion of the statistical value of the selected loci as well as the tradeoff between using highly polymorphic markers versus markers with less polymorphism is warranted. Was the selection of markers tailored to the methods that the authors intended to use, or were analysis methods selected post hoc? In general however, I agree that the selected markers exhibit a degree of polymorphism well matched to the sample sizes that were available, with the possible exception of Ots-l 03, for which the number of alleles is larger than the sample size for some groups.

The use of the programs KINSHIP and SIBLINGS allowed for a much more statistically rigorous examination of the genetic relationships of individuals within subgroups, and hence allowed for potentially more robust tests of differentiation/relatedness of subgroups and spawning aggregates. However, a discussion of the assumptions required by SIBLINGS, as well as the potential biases introduced by the use of this program is lacking.

Beyond the use of the program SffiLINGS, the analysis of the resulting hypothetical parental and unrelated samples is straightforward and sufficient for the purpose of the report. However, there are some additional analytical tools that might aid in interpretation of the results. For example, the program MIGRATE (Beerli and Felsenstein 2001) could be used as an alternative method for computation of effective population sizes, and additionally could be used to estimate rates of migration between spawning aggregates. For many of the key questions it might be useful to use a number of methods, each with different assumptions, to calculate the quantity of interest. Doing so would erase any doubt that a given result is method dependent and indicate whether results are robust regardless of the methodology used and the assumptions required (and potentially violated).

Biological Evaluation

Some basic life-history characteristics of coho could be discussed in more detail. For example, throughout their range, coho exhibit a relatively fixed three-year life cycle. So, one might expect greater temporal variation between repeated samples from a coho spawning aggregate than for other Pacific salmonids (e.g., chinook salmon) for which overlapping generations might have the effect of decreasing temporal variation within a spawning aggregate. While this feature of coho salmon life history is probably not an adequate explanation for the F ST values observed between temporal samples from some of the spawning aggregates, it could explain at least a portion of that variation. This is particularly true for the "jack" versus adult samples analyzed from the Trinity River Hatchery.

Regarding the congruence of geography and genetics, the authors should consider a discussion of documented straying among coho spawning aggregates from the Pacific Northwest (rather than dismissing the potential contribution of strays to a Wahlund effect - the stated alternative to inbreeding as an explanation for high rates of observed linkage disequilibrium). This is a particularly important point for Green Valley samples, given the history of different broodstock sources potentially introduced to this area from hatchery programs. Additional ancillary data suggest that the assumption that decreased fitness of hatchery stocks may have precluded their contribution to natural production may be faulty. For example, in the Columbia River Basin, reintroductions of coho salmon in the upper Columbia and Snake Rivers, using downriver hatchery stocks, has been enormously successful, suggesting one or more of several alternatives; that coho exhibit a remarkable degree of plasticity, are not as prone to large fitness differentials resulting from local adaptation, and/or are not as greatly effected by hatchery rearing as other species of Pacific salmon. However, these data are available only in the form of "white" papers, and hence are not part of the accessible pool of peer-reviewed literature.

Finally, in an attempt to minimize linkage disequilibrium, the researchers decomposed sample groups into a number of subgroups, some of which were clearly justifiable, but others that are biologically questionable. For example, separating "jack" coho from other adult coho at the Trinity River Hatchery has a biological basis, given that they are of different cohorts, and hence arise from temporally isolated parental populations. Alternatively, it is not at all clear that binning samples based on capture date from the lower South Fork trap on the Little River is biologically justifiable (it may be, but some justification is required). The same is true for the ESPRS99 sample group (which was subdivided based on a size gap ftom92 to 96 mm, which could potentially be explained by a few days difference in emergence and growth) and the MATS sample group (subdivided based on apparently arbitrary binning of capture dates). Again, there could be credible biological justification for these subdivisions, but it is not provided.

Interpretation of the Results

Overall, it is my opinion that the researchers present an unbiased interpretation of the results, although the management ramifications of their interpretations could be discussed in greater detail. I agree that the data indicate that the Eel, Russian (Green Valley), and Noyo River samples all exhibit high within group relatedness (e.g., high probability of inbreeding), and that this interpretation is a more plausible, and better supported, explanation for observed linkage disequilibrium than the Wahlund effect. In general, sample groups exhibited high levels of relatedness, however the authors' assertion that inbreeding depression may be contributing to the decline of the species cannot be directly addressed with these data without ancillary information.

I agree with the authors that the Green Valley coho spawning aggregate exhibits a high degree of relatedness, thus the authors rightfully express concern regarding a program that derives broodstock solely from a (apparently) highly inbred population. However, I am confused by the parting statement that "this small population appears to be anomalous and unrepresentative of the Central California ESU." What is intended by this comment? Does its distinctiveness make this spawning aggregate critical for conservation, or are the authors suggesting that recovery efforts for this "anomalous" population should be abandoned?

Conclusions

The stated objectives for this research included: I) to determine relatedness in samples comprised of juveniles; 2) to determine temporal genetic variation within year classes; 3) to estimate genetic divergence among and effective population sizes of spawning runs; 4) to determine genetic change between historical and extant coho populations; and 5) to relate the genetic diversity of California coho populations to environmental and biological factors being measured in the sampling process. In general, objectives one, two, and three were satisfied, with the exception that available samples limits my faith in the interpretation of results, and with the exception that effective population size was dealt with explicitly only for the Green Valley sample group. Objective four was not addressed, and could not be addressed with the samples that were analyzed. Objective five also was not addressed, but should be given that the interpretation of results relies on the ability of the samples to represent biological reality.

Some puzzling statements were included in the report. For example, the authors suggest that the results support existing ESU designations, but this assertion appears inconsistent with the research completed by Kate Bucklin that found "very little" variation at the nucleotide level. Perhaps more detail could explain the potential discrepancy.

Finally, while it is arguably outside the scope of the contracted work, the authors undoubtedly are in the best position to suggest management alternatives from a genetic standpoint. While management decisions for California coho cannot, and should not, be based solely on genetic considerations, the researchers could provide more directed management guidance. A statement relaying the faith that the authors place in the results would be helpful.

PART II: STEELHEAD ANALYSES

Apparently none of the objectives for steelhead were completed. In addition, the proposed research into candidate genes controlling run timing, while interesting, would have been unlikely to address all listed study objectives.

PART III: CHINOOK SALMON

Introduction

Similar to the review of coho analyses, I have structured comments regarding the analyses pertaining to chinook salmon as statistical, biological, and interpretation. Also, as with the coho analyses, it is unclear why sample sizes and replication of sample groups is less than desirable. Two of the largest sample groups (Warm Springs Hatchery adults samples from 1997) were excluded from analyses based on high rates of observed linkage disequilibria. Are the authors comfortable that the samples made available for analysis adequately represent genetic variation, and hence can be used as a basis for biologically meaningful management decisions?

Statistical

The analyses employed by the researchers to address genetic variation and differentiation among the sampled groups of chinook salmon would be acceptable if sample sizes and temporal replicates were available. However the sample sizes available, and the temporal distribution of those samples decreases my faith in the resulting analyses (see "biological" comments). The researchers emphasize that the resolved Russian River samples cluster together (bootstrap value of 848/1000), but are "distinct" from Eel River samples (bootstrap value of 919/1 000), this is a problematic statement for two reasons.

First, given that the Forsyth 1999 sample group was not significantly distinguishable from either Russian River sample group it is not clear why the Forsyth samples were grouped with the Mirabel 2000 samples (why not group them with the Mirabel 1999 samples, or better yet treat them independently?). In this case it might be useful to review the sources of genetic sampling error that might obscure comparisons. Within the Russian River samples for example, eight adult samples from 1999 were grouped with 82 juvenile samples from 2000. We might expect that such a grouping would potentially increase genetic distance between the 1999 Mirabel juvenile sample and the combined 1998 Forsyth adult/2000 Mirabel juvenile sample. In essence, temporal variation might be introduced by the grouping of juvenile and adult samples, as well as grouping samples from different geographic locations (Mirabel versus Forsyth). Although both sources of variation were shown to be insignificant when treated independently, it is possible that the respective errors, when treated concurrently by grouping samples, could contribute to the perceived distinctiveness in further tests (e.g., Mirabel2000/Forsyth 1999 versus Mirabel 1999). Unless there is a good reason to group the Mirabel 2000 and Forsyth 1999 sample, I would recommend treating them separately.

Second, adults from the Eel River are being compared to juveniles (and a few adults) from the Russian River. Aside from the fact that the authors suggest this is less than ideal situation; at least in regards to the coho analyses, there are reasons to believe such a comparison for these samples is problematic. Foremost, there is potential for temporal variation to obscure the relationship between Eel River adults and Russian River juveniles. Eel River adults likely arose from spawning in 1993 through 1996, while Russian River juveniles likely arose from spawning in 1998 and 1999. Up to six years of genetic drift (likely exacerbated by small and declining population size) separates these sample groups. While the Eel River spawning aggregates appear to be temporally stable, as evidenced by non-significant differentiation between adults sampled in 1998 and 1999, such stability is apparently not exhibited by Russian River spawning aggregates, as evidenced by significant temporal variation between smolts sampled from Mirabel in 1999 and 2000. How much of the perceived differentiation between these groups could be assigned to temporal variation?

In short, the researchers likely embarked on a series of exploratory analyses that led them to group samples for the final analyses presented in this report. For the reader, it might be useful to show the results of these analyses, or to describe them in more detail. Finally, I would recommend that that the authors present a Cavalli-Sforza and Edwards UPGMA dendrogram that shows the genetic relationship of ungrouped samples. If the overall result (differentiation between Eel and Russian River samples) is supported by analysis of ungrouped samples, interpretation would be more straightforward.

Biological

Regardless of statistical methods employed, the utility of genetic analyses relies on how well samples represent a population of interest. It is not at all clear that the chinook salmon samples used in these analyses are capable of expressing the range of temporal and geographic variation that is exhibited within and among the sampled spawning aggregates. As mentioned above, the most biologically troubling aspect of this analysis is the comparison of temporally distant samples from the Eel and Russian Rivers.

Interpretation

The major finding of this research is that chinook salmon collected in the Eel River appear to be distinct from chinook salmon collected in the Russian River. Whether this result is biologically meaningful remains questionable.

Conclusion

This report was intended to address two tasks: 1) establishment of a genetic baseline for chinook salmon populations from Mendocino and Sonoma counties, and comparison of those spawning aggregates to known spawning aggregates and 2) to determine the relationship between Russian River and other coastal chinook spawning aggregates including both extant and historical population samples from drainages such as the Eel River. The second task was apparently not addressed by this research, and the first task, while underway, in my opinion is incomplete. It would be helpful if the authors provided a definition for what constitutes a "genetic baseline." My definition, which is only one interpretation, would be a series of samples which when analyzed would yield an estimate of the temporal and geographic variation exhibited by chinook spawning aggregates within a watershed of interest. To construct such a baseline would require temporally repeated samples (ideally taken annually for an entire generation) from geographic locations within a watershed known to support spawning. Comparing such baselines from a number of watersheds would allow a robust construction of the relationships between stocks on a larger geographic scale. Data presented in this report are therefore a good start to such a baseline, but fall short of my definition. As such, the conclusions reported by the researchers are potentially effected by some unknown degree by temporal and/or geographic variation that may not have been measured.

OVERALL CONCLUSIONS

The objective of this review was to determine whether contractual obligations were satisfied by this research. With regard to coho salmon, I would say that the researchers have satisfied their obligation, with the caveats mentioned below. Steelhead objectives have not been achieved, at least as presented here, nor have the objectives for chinook salmon been achieved. Each of the previous statements, however must be bounded by the caveat that a laboratory can only analyze the samples that are received. In general, this research, and the conclusions that can be drawn from the analyses, is severely limited by sample availability.

Aside from sampling considerations, this report would greatly benefit from increased detail regarding the researchers faith in the results. Are the authors convinced that the results of their analyses are biologically meaningful, or do they feel that the results are constrained by sample availability to a degree that limits their utility for management? Given that the researchers are in arguably the best position to provide management guidance from a genetic perspective, it would be useful (and a departure from the ordinary) for them to include a section detailing their respective opinions regarding management.

Finally, the GIS applications as well as the research into alternative male coho phenotypes was not linked to specific contractual obligations - despite the fact that both of these data types could be potentially provide guidance to data analysis.

Literature Cited

Beerli, P. and J. F elsenstein (2001) Maximum likelihood estimation of a migration matrix and effective population sizes in n subpopulations by using a coalescent approach. PNAS 98(8): 4563-4568.